Safety and Efficacy Study of Apremilast to Treat Psoriatic Arthritis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of Apremilast to Treat Psoriatic Arthritis (NCT01925768), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Achieved an American College of Rheumatology 20% (ACR20) Response at Week 16.

2. Clinical Question

3. Trial Design

The registry record describes a phase 3b, multicenter, randomized, double-blind, placebo-controlled, parallel-group study of apremilast monotherapy in participants with active psoriatic arthritis. The recorded masking designation is quadruple. The study enrolled 219 participants, with 109 assigned to placebo and 110 to apremilast 30 mg for the primary outcome. The registry lists the study as completed.

The recorded study start date is 2013-09-04 and the primary completion date is 2015-02-25. During the placebo-controlled phase, the apremilast arm received 30 mg twice daily for 24 weeks, while the placebo arm received placebo twice daily over Weeks 0 to 24. The apremilast arm description also records continued active treatment up to the Week 52 visit. The available placebo-arm description notes that some participants could be eligible for early escape at Week 16, but the full operational details of that provision are not reported in the registry record.

The primary outcome was assessed at Week 16, before the end of the placebo-controlled phase. Secondary outcomes include measures of physical function, disease activity, and response at Week 24. The registry lists 22 outcome measures and 19 analyses; 21 secondary outcomes are posted. These counts describe the record, but do not by themselves establish which results were prespecified as confirmatory or how the analyses were prioritized.

The registry record does not report the trial’s original sample-size justification, the detailed statistical analysis plan, or whether interim analyses were conducted. Those omissions limit what can be concluded about the original design choices and the role assigned to each analysis.

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: Randomized participants were stratified by their baseline prednisone use (yes or no) and by their previous disease modifying antirheumatic drug (DMARD) use (excluding biologics). Participants were allowed to take non-steroidal anti-inflammatory agents and/or low dose corticosteroids during the study.

Placebo-controlled Phase (Week 0 - 24)

Reasons for not completing this period:

ActiveTreatment/Extension (Weeks 24-104)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) population consisting of all participants randomized as specified in the protocol.

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: Full analysis set consisting of all participants who were randomized as specified in the protocol.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Achieved an American College of Rheumatology 20% (ACR20) Response at Week 16, measured over Baseline and Week 16.

The primary endpoint is the percentage of participants who achieved an American College of Rheumatology 20% response, or ACR20, at Week 16. It is a binary response measure: each participant is classified as a responder or non-responder according to the endpoint definition, and the group result is expressed as a percentage.

To qualify, a participant had to meet all three parts of the definition: at least 20% improvement from baseline in the 78 tender joint count; at least 20% improvement in the 76 swollen joint count; and at least 20% improvement in at least three of five other measures. Those additional measures cover patient assessments of pain, disease activity, and physical function, a physician assessment of disease activity, and C-reactive protein. Participants who withdrew early or did not have sufficient Week 16 data were counted as non-responders.

As a general statistical concept, a composite response endpoint combines several kinds of information into one clinically interpretable classification. It can capture improvement across multiple aspects of a condition, but it also means that the overall response rate does not show which component drove the classification. ACR20 therefore answers a defined question about the proportion meeting the combined threshold; it does not describe every participant’s degree of change or every disease feature separately.

7. Results Posted in the Registry

• Apremilast (APR) 30 mg: 38.2% (42/110) versus 20.2% (22/109) on control; risk difference 18.0 percentage points (95% CI 6.2 to 29.8), risk ratio 1.89 (1.22–2.95); unadjusted two-proportion z-test p = 0.003.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline in Health Assessment Questionnaire-Disability Index (HAQ-DI) at Week 24

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Apremilast (APR) 30 mg: mean -0.27 versus -0.17 on control; difference -0.10 (95% CI -0.26 to 0.06), standardized effect d = -0.17; z-test p = 0.202.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Apremilast (APR) 30 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Achieved an American College of Rheumatology 20% (ACR20) at Week 24

• 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:
  • Apremilast (APR) 30 mg: 43.6% (48/110) versus 24.8% (27/109) on control; risk difference 18.9 percentage points (95% CI 6.6 to 31.2), risk ratio 1.76 (1.19–2.60); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Apremilast (APR) 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the 28-Joint Disease Activity Score Using C-reactive Protein as the Acute-Phase Reactant (DAS28 [CRP]) at Week 24

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Apremilast (APR) 30 mg: mean -1.26 versus -0.76 on control; difference -0.50 (95% CI -0.89 to -0.11), standardized effect d = -0.35; z-test p = 0.011.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Apremilast (APR) 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover response at Week 24, physical function, disease activity, and other aspects of health status. Taken as a group, the available comparisons show a mixed but generally supportive pattern: some response and disease-activity measures favor apremilast, while the physical-function estimate is more uncertain. This pattern provides additional context around the primary result, but it does not make the secondary outcomes equivalent to the prespecified primary question.

Secondary outcomes often answer related but distinct questions. A response threshold, a change in a function score, and a change in a disease-activity score measure different features and use different scales. Agreement across some outcomes can add context; disagreement or imprecision can reflect real differences in the measured domains, statistical uncertainty, or both. The registry record does not supply participant-level results that would explain those patterns.

Many outcomes were posted, and the record lists 21 secondary outcomes. When multiple outcomes are tested, the chance of at least one apparently unusual result can increase if each is judged separately without adjustment. Whether a multiplicity procedure was planned or applied is not reported in the registry record. Consequently, unadjusted secondary p-values carry less weight than the primary analysis and should not be read as a set of independent confirmatory findings.

The secondary results therefore complement rather than replace the Week 16 ACR20 comparison. Their value is in showing how the observed pattern extends across other recorded measures and time points, while their multiplicity and distinct measurement properties limit the strength of broader claims.

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

• Change From Baseline in Health Assessment Questionnaire-Disability Index (HAQ-DI) at Week 24
• Percentage of Participants Who Achieved an American College of Rheumatology 20% (ACR20) at Week 24
• Change From Baseline in the 28-Joint Disease Activity Score Using C-reactive Protein as the Acute-Phase Reactant (DAS28 [CRP]) at Week 24
• Change From Baseline in the Medical Outcomes Short Form Health Survey (SF-36) V2 Physical Function Domain Score at Week 24
• Change From Baseline in the 36-item SF-36 Physical Component Summary Score at Week 24
• Change From Baseline in the Duration of Morning Stiffness at Week 24
• Percentage of Participants With Improved Change in Severity of Morning Stiffness at Week 24
• Change From Baseline in Health Assessment Questionnaire-Disability Index (HAQ-DI) at Week 16

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary because each participant either meets the ACR20 response criteria at Week 16 or does not. The registry gives the percentage in each randomized group and reports a Cochran-Mantel-Haenszel analysis of the adjusted difference. The separate recalculation uses the posted group summaries to estimate an unadjusted risk difference. These are related but not identical analyses: the first is the sponsor’s reported adjusted analysis, while the second is a simple comparison of the observed proportions.

What does an adjusted difference mean?

The sponsor’s reported method is Cochran-Mantel-Haenszel. In general, this method can combine comparisons across strata to produce an adjusted estimate, rather than treating the overall groups as an unstratified comparison. The registry record does not identify the stratification factors used for this result, so their identities and their influence on the estimate are not reported in the registry record. The method name alone does not establish which covariates were included or how randomization factors were handled.

The sponsor reports an adjusted difference of 17.7, a 95% confidence interval from 6.2 to 29.3, and p = 0.004. The simple unadjusted recalculation reports a risk difference of 0.18, a 95% confidence interval from 0.062 to 0.298, and p = 0.003. The recalculation is not a replacement for the study’s analysis. It is a transparent comparison derived from the posted counts and provides a check on the broad direction of the result.

How should the p-value be read?

As a general statistical explanation, a p-value measures how unusual data at least as inconsistent with a specified null model would be if that model and the analysis assumptions were correct. It does not give the probability that the null hypothesis is true, and it does not measure the magnitude or practical importance of an effect. The sponsor’s p-value is attached to its adjusted analysis; the recalculated p-value is attached to the unadjusted comparison. They should not be treated as interchangeable outputs from one procedure.

The confidence interval describes uncertainty around an estimated difference. In general, a 95% confidence interval is generated by a procedure that, over repeated comparable studies under its assumptions, would cover the target parameter in 95% of intervals. For an individual trial, it gives a range of values compatible with the data and analysis, not a guarantee that the true value lies inside it. The sponsor’s interval for the adjusted difference is above zero, which is consistent with a positive adjusted difference under that analysis.

What do the continuous secondary analyses report?

The HAQ-DI and DAS28 [CRP] outcomes are continuous change-from-baseline measures. Their registry results are presented as least-squares means with standard errors, and the sponsor reports mixed-model analyses of least-squares mean differences. In general, a least-squares mean is a model-based estimate, and a mixed model can account for the structure of repeated or otherwise related observations. The registry record does not report enough model detail to describe the covariates, covariance structure, or missing-data assumptions used in these analyses.

For the HAQ-DI comparison, the sponsor reports a least-squares mean difference of -0.103, with a 95% confidence interval from -0.251 to 0.044 and p = 0.168. For DAS28 [CRP], the reported difference is -0.50, with a 95% confidence interval from -0.85 to -0.15 and p = 0.005. The signs must be interpreted in the context of each outcome’s direction and change-from-baseline definition; they are not directly comparable with the binary ACR20 difference. The registry record does not give a single common scale for weighing these outcomes against one another.

Why can over-dispersion matter?

General statistical explanation: binary outcomes are often analyzed using models that assume a particular relationship between the mean response and its variability. Over-dispersion occurs when the observed variation is greater than the model allows. If it is ignored, uncertainty can be understated and inference can become too optimistic. The registry record does not identify an over-dispersion assessment for the primary analysis, so it is not possible to say whether it was evaluated or how it would affect the reported result.

For continuous outcomes, standard errors describe uncertainty in estimated means or differences, while standard deviations describe variation among individual observations. The secondary outcome records specify standard errors for least-squares means. The recalculated standardized effect for some outcomes uses an approximate pooled standard deviation derived from posted summaries; it is an unadjusted approximation, not a substitute for the sponsor’s model-based analysis. The posted sponsor analyses remain the principal reported inferential results for those endpoints.

Finally, analysis population and endpoint rules affect interpretation. The primary population is the Full Analysis Set, defined as all randomized participants specified by the protocol. Counting early withdrawal or insufficient Week 16 information as non-response is an explicit primary endpoint rule. Other details about the handling of missing values in the secondary analyses are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor’s 95% confidence interval for the adjusted Week 16 ACR20 difference runs from 6.2 to 29.3. The interval lies above zero, so the reported adjusted analysis is consistent with a positive difference between groups. Its width also matters: the estimate is not precise enough to identify one exact magnitude, and a range of positive effects remains compatible with the analysis.

The simple recalculation gives a 95% confidence interval from 0.062 to 0.298 for the unadjusted risk difference. This interval is also above zero. It should be interpreted on the scale of that recalculation and not confused with the sponsor’s adjusted percentage-scale estimate. Differences between the two estimates can reflect their distinct scales and analytic approaches; the registry record does not report a direct reconciliation of the methods.

As a general explanation, confidence intervals communicate both direction and uncertainty. An interval excluding zero is evidence against a zero difference under the model used to construct it, but the interval does not establish that every value inside it is equally plausible. Nor does it indicate whether a difference is important to patients or clinicians. Those judgments require context beyond a statistical interval.

For the secondary results, the HAQ-DI sponsor interval includes zero, while the reported intervals for ACR20 at Week 24 and DAS28 [CRP] do not. These outcomes differ in measurement, timing, and analysis, so their intervals should be read endpoint by endpoint. The registry record does not report a multiplicity adjustment that would convert all the intervals into a family of simultaneous confidence intervals.

Precision is also constrained by the number of participants contributing to each outcome and by the amount of information captured in the summary. The primary analysis includes 109 participants in the placebo group and 110 in the apremilast group. For secondary outcomes, the analyzed group counts vary. Summary estimates cannot show the full distribution of participant-level responses or reveal whether particular subgroups have different effects.

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 expressed as participants per arm. They are not total event counts: this is not a time-to-event outcome. The listed 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 trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm that the calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations, not probabilities that the completed trial’s result is correct and not assessments of the trial’s achieved power.

The rows represent planning for the full observed effect and for smaller fractions of that effect. Smaller effects are harder to distinguish from random variation, so the calculation calls for more participants per arm as the target effect becomes smaller. The displayed numbers should therefore be understood as conditional illustrations: changing the target effect or planning assumptions would change the estimated sample size.

This is not observed power. Observed power is sometimes calculated from a completed study’s estimated effect, but it does not provide a useful independent measure of the evidence once the result and its uncertainty are known. The confidence interval and the study’s reported analysis are more informative for interpreting the completed trial. The planning figures also do not demonstrate that the original study was designed to detect the observed effect, because its original design rationale is 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 = 0.202; treatment proportion p₁ = 0.382; average p̄ = 0.292.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6429 = 1.2601.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6302 = 0.5304.
4. n = (1.2601 + 0.5304)² / (0.1800)² = 99.0, rounded up to 99 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 <- 0.201834862385321                          # control proportion
p1 <- 0.381818181818182                          # 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(1925768)
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 = 99 (80% power), 132 (90% power)
 75% of observed effect: n per arm = 169 (80% power), 225 (90% power)
 50% of observed effect: n per arm = 360 (80% power), 481 (90% power)
power.prop.test: 99 
Simulated power at n = 99 per arm: 0.805 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis uses the Cochran-Mantel-Haenszel method and reports an adjusted difference of 17.7, with a 95% confidence interval from 6.2 to 29.3 and p = 0.004. This is the study’s reported adjusted inferential result for the Week 16 ACR20 endpoint. The registry record does not identify the adjustment strata or provide further detail about the analysis specification.

The unadjusted recalculation uses the posted group response summaries and reports a risk difference of 0.18, a 95% confidence interval from 0.062 to 0.298, and p = 0.003. It does not reproduce the sponsor’s adjustment. The estimates are presented on different scales, so their numerical values should not be compared as if they were the same quantity in the same units. Both point in the same broad direction, but the sponsor’s analysis remains the primary reported analysis, while the recalculation is a simple descriptive check.

For the secondary continuous outcomes, the sponsor reports mixed-model analyses, while the recalculations use unadjusted comparisons of posted summaries. The two approaches can differ because they use different models and assumptions. The recalculated results should not be treated as corrections to, or replacements for, the sponsor’s analyses. When describing the trial’s own inferential findings, the sponsor-reported estimates and methods are the appropriate reference point.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple endpoints, time points, or comparisons. General statistical explanation: if many hypotheses are tested and each is judged at the same nominal threshold, the chance of at least one false-positive result across the family can rise. Procedures such as hierarchical testing or adjustment of p-values can address particular multiplicity structures, but the choice depends on which outcomes are treated as confirmatory and how the testing sequence is defined.

The registry record lists 22 outcome measures, 19 analyses, and 21 posted secondary outcomes. It does not report whether a multiplicity adjustment was used, which outcomes belonged to a confirmatory family, or whether testing followed a prespecified hierarchy. The presence of several favorable secondary comparisons should therefore not be interpreted as if each were an independent confirmation. The primary Week 16 endpoint has a clearly identified role in the record; the broader status of the secondary analyses is less clear.

The primary endpoint definition specifies that participants who withdrew early or lacked sufficient Week 16 data were counted as non-responders. This rule gives the primary response analysis a defined treatment of those cases. The primary analysis population is the Full Analysis Set, described as all participants randomized as specified in the protocol. The registry record does not report detailed counts of missing Week 16 observations or the sensitivity analyses used to assess the effect of this rule.

Missing-data methods for the secondary outcomes are not reported in the registry record. The reported analyzed numbers vary across some outcomes, but those counts alone do not establish why values were unavailable or how missing observations were handled. The registry record also does not report the complete statistical analysis plan, the rationale for the primary analysis model, or whether interim analyses took place. These omissions limit assessment of prespecification and robustness; they do not, on their own, establish that a particular method was or was not used.

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 (1.0%), iron deficiency anaemia (0.9%), angina pectoris (0.9%), chest pain (0.9%), biliary colic (0.9%).

For the placebo-controlled phase, the registry lists serious adverse events affecting 5 of 109 participants in the placebo group and 3 of 109 in the apremilast group. A separate apremilast exposure-period record lists 15 of 206 participants with a serious adverse event. The exposure-period figure covers a different group and period from the placebo-controlled comparison, so it should not be read as a direct randomized comparison with the placebo figure.

The registry lists serious-event terms and their percentages, including coronary artery disease at 1.0%, and iron deficiency anaemia, angina pectoris, chest pain, biliary colic, and cervical vertebral fracture at 0.9% each. These are recorded event terms, not evidence that the study established a cause. The registry does not report a death count in the posted serious-event summary.

Serious adverse event counts do not describe all adverse events, their severity distribution, timing, or whether investigators considered them related to treatment. The posted counts should be interpreted within the specified exposure periods and denominators. They do not by themselves provide a complete comparative safety assessment.

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

The primary result describes a difference in the proportion of randomized participants who met the defined ACR20 response criteria by Week 16. The recorded response percentage was higher in the apremilast group than in the placebo group, and the sponsor’s adjusted confidence interval lies above zero. This is evidence of a between-group difference for that endpoint and time point under the reported analysis.

The result does not establish the size of benefit for every individual participant. A group response percentage does not show the range of individual changes, identify which components of ACR20 were most influential, or indicate how participants who did not meet the threshold experienced their disease. It also does not establish an effect on outcomes that were not measured or reported.

The result is specific to the enrolled participants, the apremilast 30 mg regimen, the placebo-controlled comparison, and the Week 16 assessment. The registry record describes an active-treatment period extending up to the Week 52 visit for the apremilast arm, but the primary result is not a Week 52 comparison. It should not be used to infer the same comparative effect at later times.

Statistical evidence and clinical importance are separate considerations. A confidence interval and p-value describe uncertainty under an analysis; they do not determine whether the observed difference is meaningful for patients. The registry record does not supply a threshold for clinical importance for the primary endpoint. Nor does the result alone resolve questions about long-term outcomes, differences among participant subgroups, or the balance of benefits and harms.

The secondary outcomes add perspective but include multiple measures, and the registry record does not describe a multiplicity strategy. They should be interpreted as additional reported evidence with their own uncertainty rather than as a substitute for the primary endpoint or as conclusive evidence for every outcome domain.

18. Why This Trial Matters Statistically

This trial illustrates why the estimand and endpoint definition matter. ACR20 is not simply a count of improved joints: it combines tender and swollen joint-count thresholds with improvement in a subset of additional measures. The primary result therefore refers to meeting a specific composite threshold, and the rule counting early withdrawal or insufficient Week 16 information as non-response is part of what that result means.

It also demonstrates the distinction between an adjusted sponsor analysis and a simple recalculation from group summaries. The sponsor reports a Cochran-Mantel-Haenszel adjusted difference, while the recalculation compares observed proportions without that adjustment. Both are useful to recognize, but they answer the inferential question through different analytic routes. Keeping the reported analysis separate from a summary-statistic check prevents a recalculation from being mistaken for the trial’s original analysis.

Precision matters alongside statistical significance. The primary confidence interval remains a range of compatible positive differences, not a single definitive magnitude. Secondary outcomes add breadth but also raise questions about multiplicity, especially when many endpoints and time points are recorded and the analysis hierarchy is not reported.

Finally, safety summaries require attention to exposure period and denominator. The placebo-controlled counts and the longer apremilast exposure-period count do not represent the same randomized comparison. This is a useful reminder that a count of adverse events is meaningful only in context: who was observed, for how long, and under which treatment assignment all matter.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not include the full statistical analysis plan, original sample-size justification, or details of interim analyses. It also does not report the stratification factors used in the primary Cochran-Mantel-Haenszel analysis. These gaps make it difficult to assess how closely the reported analyses follow the original plan or to reproduce the adjusted result from the record alone.

The primary endpoint is assessed at Week 16 and uses a threshold-based composite response. That summary does not show component-specific response patterns or the distribution of continuous changes. The explicit non-responder rule for early withdrawal or insufficient data is reported, but counts and sensitivity analyses concerning missing Week 16 data are not reported in the registry record.

The available secondary results cover numerous outcomes, and the record does not report a multiplicity strategy. Their inferential strength is therefore harder to evaluate as a family. For continuous secondary measures, the registry gives model-based estimates but not the detailed model specifications or missing-data assumptions. Unadjusted recalculations from summaries may also differ from the sponsor’s model-based estimates.

The posted safety summary separates the placebo-controlled phase from a broader apremilast exposure period. Those records have different denominators and exposure contexts, so they cannot be treated as one like-for-like randomized comparison. The registry’s serious-event summary also does not provide a complete account of all adverse events or their attribution.

Finally, the primary comparison is confined to the recorded study population, regimen, comparator, and time point. The registry record alone cannot establish how the results apply to populations, treatment settings, or outcomes not represented in the study.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of Apremilast to Treat Psoriatic Arthritis — NCT01925768.
• Registry record last updated 2020-05-12; status last verified 2020-04.
• Results first posted 2016-06-13.
• 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

NCT01925768 is a completed phase 3b, randomized, quadruple-masked, parallel-group, placebo-controlled study of apremilast monotherapy in active psoriatic arthritis. The record lists 219 enrolled participants and compares apremilast 30 mg with placebo during the placebo-controlled phase.

The primary endpoint is Week 16 ACR20 response. The sponsor reports an adjusted difference of 17.7, with a 95% confidence interval from 6.2 to 29.3 and p = 0.004. The simple unadjusted recalculation is directionally consistent but uses a different scale and analysis. Secondary results broaden the set of measured outcomes, while multiplicity and analysis details are not fully reported.

The primary response result is specific to its endpoint definition and time point. Safety counts should be read within their distinct exposure periods, and neither the primary nor secondary summaries answer questions beyond the outcomes and analyses recorded.