Study to Examine the Clinical Efficacy and the Nonsteroidal Anti-inflammatory Drug (NSAID)-Sparing Effect of Secukinumab Over 16 Weeks in Patients With Ankylosing Spondylitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Examine the Clinical Efficacy and the Nonsteroidal Anti-inflammatory Drug (NSAID)-Sparing Effect of Secukinumab Over 16 Weeks in Patients With Ankylosing Spondylitis (NCT02763046), a randomized phase 4 study. The primary outcome is Proportion of Patients Who Achieved ASAS20 Response in the Pooled Secukinumab Group Compared With the Placebo Group at Week 12.

2. Clinical Question

3. Trial Design

The registry describes NCT02763046 as a completed Phase 4, randomized, triple-masked, parallel-group study sponsored by Novartis Pharmaceuticals. Its title identifies secukinumab and the NSAID-sparing effect in patients with ankylosing spondylitis as the focus. The registry lists enrollment as 211. The trial’s primary endpoint compared pooled secukinumab with placebo at Week 12.

The study included secukinumab groups with delayed and early NSAID tapering, as well as a placebo group. The secukinumab regimen for the delayed-tapering group began with weekly injections and then moved to injections every four weeks. In the early-tapering group, placebo injections preceded secukinumab induction, followed by maintenance dosing. The placebo group received placebo during the primary assessment period and then received secukinumab after the Week 16 assessments of the secondary endpoint. These details describe the registry-listed treatment sequence; the original protocol’s full operational details are not reported in the registry record.

The registry’s brief summary says participants first had a run-in phase of stable NSAID therapy. NSAID tapering was allowed from Week 4 in the placebo group, and the delayed-tapering arm description also states that tapering was allowed from Week 4, although its description is truncated. The registry records several secondary outcomes, including ASAS-NSAID score, BASDAI total score, and SF-36 physical component score. The trial’s original statistical plan, sample-size justification, and detailed handling of each secondary endpoint are not reported in the registry 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.

Before assignment: Participants were randomized 1:1:1 to one of the following treatment groups: secukinumab 150 mg s.c. with delayed NSAID tapering, secukinumab 150 mg s.c. with early NSAID tapering and placebo.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) comprising all subjects from the randomized set to whom study treatment was assigned.

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 Proportion of Patients Who Achieved ASAS20 Response in the Pooled Secukinumab Group Compared With the Placebo Group at Week 12, measured over Baseline, Week 12.

The primary endpoint was the proportion of participants who achieved an ASAS20 response in the pooled secukinumab group compared with placebo at Week 12. ASAS20 is a binary outcome: a participant either meets the response definition or does not. The definition requires improvement from baseline of at least 20% and at least one unit on a scale of 0 to 10 in at least three of the four ASAS domains, with no worsening meeting those thresholds in the remaining domain. The domains cover the patient’s global assessment of disease activity, back pain, function, and inflammation.

A composite response measure combines several areas of disease assessment into a single endpoint. This can make a result easier to interpret as the proportion meeting a prespecified response definition, while also meaning that different patterns across the component domains are compressed into one classification. The endpoint was used to assess clinical response, while the trial also investigated whether NSAID treatment could be reduced. The ASAS20 result alone does not describe the amount of NSAID reduction.

The registry states that non-responder imputation was applied for missing primary-endpoint data. Under this approach, participants with missing response information are classified as non-responders for the analysis. The exact count of missing primary-endpoint observations is not reported in the registry record.

7. Results Posted in the Registry

• Secukinumab - Pooled: 51.1% (72/141) versus 44.3% (31/70) on control; risk difference 6.8 percentage points (95% CI -7.5 to 21.0), risk ratio 1.15 (0.85–1.57); unadjusted two-proportion z-test p = 0.354.

8. Secondary Efficacy Endpoints

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

Mean Change From Baseline in ASAS-NSAID Score at Week 12

• 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:
  • Secukinumab - Delayed NSAID Tapering: mean -44.90 versus -31.50 on control; difference -13.40 (95% CI -27.34 to 0.54), standardized effect d = -0.32; z-test p = 0.060.
  • Secukinumab - Early NSAID Tapering: mean -40.30 versus -31.50 on control; difference -8.80 (95% CI -27.61 to 10.01), standardized effect d = -0.16; z-test p = 0.359.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Secukinumab - Delayed NSAID Tapering and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Secukinumab - Early NSAID Tapering and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in ASAS-NSAID Score in Each Secukinumab Group After 12 Weeks of Exposure (at Week 12 in the Secukinumab-delayed NSAID Tapering Group and at Week 16 in the Secukinumab-early NSAID Tapering Group)

• 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:
  • Secukinumab - Early NSAID Tapering: mean -42.50 versus -44.90 on control; difference 2.40 (95% CI -17.08 to 21.88), standardized effect d = 0.04; z-test p = 0.809.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Secukinumab - Early NSAID Tapering and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in Health-related Quality of Life as Measured by the Short Form-36 Health Survey (SF-36) Physical Component Summary (PCS) Score

• 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:
  • Secukinumab - Delayed NSAID Tapering: mean 4.80 versus 4.80 on control; difference 0.00 (95% CI -2.39 to 2.39), standardized effect d = 0.00; z-test p = 1.000.
  • Secukinumab - Early NSAID Tapering: mean 6.10 versus 4.80 on control; difference 1.30 (95% CI -1.08 to 3.68), standardized effect d = 0.18; z-test p = 0.284.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Secukinumab - Delayed NSAID Tapering and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Secukinumab - Early NSAID Tapering and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover NSAID-related scores, disease activity, and health-related quality of life, with some comparisons made separately for the two secukinumab schedules. Taken together, they address additional dimensions of the study question rather than providing a single uniform confirmation of the primary ASAS20 comparison. The posted summaries show variation in the direction and precision of the observed contrasts across outcomes. The endpoint definitions, time points, and comparison groups also differ, so the values should be interpreted in their own contexts.

These secondary measures relate to the primary result by adding information about NSAID use scores and other patient or disease measures. They do not replace the primary endpoint, which was the Week 12 ASAS20 response comparing pooled secukinumab with placebo. Nor do secondary score changes directly explain which participants met ASAS20. A difference in one outcome cannot be assumed to imply a matching difference in another.

Unadjusted secondary results carry less weight when multiple outcomes or comparisons are examined. In general, testing many hypotheses increases the chance that some results will appear notable by chance, even when no corresponding underlying effect exists. Adjustment procedures or a prespecified hierarchy can help address that issue, but the registry record does not report a multiplicity strategy or a complete analysis hierarchy. Thus, the secondary p-values should be treated as exploratory signals rather than as independent definitive tests.

The number of outcome measures and analyses recorded in the registry makes it particularly important not to select one secondary result in isolation. Interpretation should consider whether the analysis was planned, how outcomes were defined, which comparison was made, and whether results are consistent across related measures. The registry record does not provide enough information to establish all of those details. The overall secondary pattern is therefore best viewed as context for the primary finding, with uncertainty and multiplicity in mind.

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

• Proportion of Patients Who Achieved ASAS20 Response in Each Secukinumab Group (Delayed NSAID Tapering and Early NSAID Tapering) Compared With the Placebo Group
• Mean Change From Baseline in ASAS-NSAID Score at Week 12
• Mean Change From Baseline in ASAS-NSAID Score in Each Secukinumab Group After 12 Weeks of Exposure (at Week 12 in the Secukinumab-delayed NSAID Tapering Group and at Week 16 in the Secukinumab-early NSAID Tapering Group)
• Mean Change From Baseline in the BASDAI Total Score
• Mean Change From Baseline in Health-related Quality of Life as Measured by the Short Form-36 Health Survey (SF-36) Physical Component Summary (PCS) Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary because it records whether each participant met the ASAS20 definition. For a binary outcome, an observed response proportion is the number meeting the definition divided by the number analyzed in that group. The registry reports 72 responses among 141 participants in the pooled secukinumab group and 31 among 70 participants in the placebo group. Missing primary-endpoint data were handled using non-responder imputation, as stated in the registry record.

What does the risk difference describe?

The risk difference subtracts the comparator group’s response proportion from the intervention group’s response proportion. It is an absolute contrast on the proportion scale. The unadjusted re-calculation gives 0.068, with a 95% confidence interval from -0.075 to 0.210. Its point estimate is positive, consistent with a higher observed proportion in the pooled secukinumab group, but the interval includes zero. A confidence interval describes a range of estimates compatible with the data under the method’s assumptions; it does not assign a probability that the true value lies at a particular point inside that interval.

Why is the registry analysis expressed as an odds ratio?

The sponsor’s reported analysis used logistic regression and reported an odds ratio of 1.32. An odds ratio compares the odds of response between groups, rather than subtracting response proportions. Its 95% confidence interval is 0.74 to 2.36, and the reported p-value is 0.351. The interval includes the value corresponding to equal odds. The registry record does not report enough detail to characterize the model’s covariates or other specifications beyond the method name and reported result.

How should the p-values be read?

A p-value assesses how incompatible the observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The re-calculated unadjusted p-value is 0.354; the registry reports p = 0.351 for its logistic-regression analysis. They are close but arise from different analyses, so the registry’s own result is the appropriate report of the sponsor’s analysis.

The unadjusted re-calculation uses posted group-level summary statistics and does not reproduce a model-based analysis. It does not account for adjustments that may have been used in the registry analysis. In general, adjustment can change an estimate or its uncertainty when the analysis accounts for additional variables or design features. The registry record does not report a detailed model specification here, so further explanation of any adjustment is not possible.

Why do analysis populations matter?

The primary population is described as the full analysis set, comprising all subjects from the randomized set to whom study treatment was assigned. This describes the group included in the endpoint analysis, but the registry record does not give a separate account of exclusions or missing observations. Non-responder imputation defines how missing primary responses were classified; it does not reveal how many observations were missing.

General statistical interpretation also depends on the endpoint definition, the population analyzed, and the analysis method. The response definition turns multiple domain measurements into a single classification, and pooling the two secukinumab schedules produces one primary contrast. The secondary outcomes address different measurements and comparisons. Their results should not be treated as equivalent replications of the primary binary endpoint.

11. Confidence Intervals and Precision

The primary re-calculated risk difference is 0.068, and its 95% confidence interval ranges from -0.075 to 0.210. The interval is wide enough to include no difference and estimates on either side of it. This means the observed group proportions do not pin down a narrow range of possible contrasts. The point estimate alone should not be read as a precise estimate of the underlying difference.

The sponsor’s logistic-regression estimate is an odds ratio of 1.32, with a 95% confidence interval from 0.74 to 2.36. The interval includes the value for equal odds and spans odds ratios on both sides of that value. Since an odds ratio and a risk difference use different scales, the numerical values of their intervals cannot be compared directly. Both intervals communicate uncertainty, but each refers to its own measure and analysis.

A confidence interval is a measure of statistical precision under the method’s assumptions, not a guarantee that the true effect is inside the interval and not a statement about clinical importance. The precision of the primary result is limited by the uncertainty reflected in the interval. The registry record does not report a prespecified clinically important difference for ASAS20, so the interval cannot be evaluated against such a threshold using the posted information.

General considerations include the number of observations, the frequency of the outcome, and how the analysis handles missing data and model structure. These can affect precision. The record states that non-responder imputation was used for missing primary-endpoint data, but does not report the missing-data count. The confidence interval should therefore be read as uncertainty for the reported analysis, not as a complete account of every source of uncertainty in the trial.

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 effect, not the trial’s original design justification. For these non-time-to-event outcomes, the figures mean participants per arm, rather than total events. The calculation assumptions listed for the illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The 80% power column indicates the participants per arm estimated by the planning calculation to provide an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect and the model assumptions held. The 90% power column expresses the same planning idea with a higher target chance of detection. These are design-planning quantities, not guarantees about a future study’s result. This is not observed power.

Rows that plan for a smaller fraction of the observed effect require more participants per arm in the illustrations. That pattern follows from the general statistical principle that smaller differences are harder to distinguish from random variation. The number of participants needed also depends on the outcome and assumptions used in a calculation, so figures from different endpoints should not be treated as interchangeable.

The registry record does not report the trial’s own sample-size assumptions or justification. The illustrations should therefore not be used to claim that the completed study was planned around the observed result, nor to infer what the original investigators anticipated. They show how hypothetical future planning changes when the target effect and stated calculation assumptions change.

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 = 0.443; treatment proportion p₁ = 0.511; average p̄ = 0.477.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7063 = 1.3844.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7047 = 0.5931.
4. n = (1.3844 + 0.5931)² / (0.0678)² = 851.2, rounded up to 852 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 <- 0.442857142857143                          # control proportion
p1 <- 0.51063829787234                          # 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(2763046)
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 = 852 (80% power), 1,139 (90% power)
 75% of observed effect: n per arm = 1,512 (80% power), 2,023 (90% power)
 50% of observed effect: n per arm = 3,394 (80% power), 4,543 (90% power)
power.prop.test: 851.2 
Simulated power at n = 852 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis used logistic regression and gave an odds ratio of 1.32, with a 95% confidence interval from 0.74 to 2.36 and p = 0.351. The unadjusted re-calculation from the posted group summaries uses the risk difference instead: 0.068, with a 95% confidence interval from -0.075 to 0.210 and an unadjusted p-value of 0.354. These are different effect measures and analyses, so the estimates are not expected to be numerically identical.

The re-calculation is a simple comparison of the posted summary statistics. It does not reproduce the sponsor’s regression model or any model specifications not described in the record. The sponsor’s own analysis takes precedence as the reported trial analysis. The close p-values do not make the methods equivalent, and neither p-value should be interpreted as the probability that there is no treatment difference.

The registry record does not report the detailed logistic-regression specification, including whether or how covariates were included. It also does not provide a complete statistical analysis plan. As a result, the sponsor result can be reported as stated, but the exact sources of any difference between an adjusted model and a simple unadjusted calculation cannot be assessed from the record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several endpoints, comparisons, time points, or analysis choices. Even if each individual test uses a conventional significance threshold, the chance of at least one apparently notable result can increase as more tests are considered. Statistical plans often address this through a prespecified testing sequence, adjustment, or an explicitly exploratory interpretation. The registry record does not report a multiplicity adjustment or a complete hierarchy for the primary and secondary analyses. The reported secondary p-values should therefore not be treated as though they were necessarily protected against multiple testing.

The primary endpoint is clearly identified as the Week 12 ASAS20 comparison of pooled secukinumab with placebo. The registry also lists secondary outcomes and multiple analyses. It is not reported in the registry record whether the primary analysis was part of a formal sequence that controlled the overall error rate or whether secondary analyses were intended to be confirmatory. Without those details, the distinction between prespecified confirmatory and exploratory secondary findings cannot be fully assessed.

For missing primary-endpoint data, the registry states that non-responder imputation was applied. This classifies missing response data as non-response in the primary analysis. The number of missing observations, reasons for missingness, and sensitivity analyses using other assumptions are not reported in the registry record. These details matter because missing-data assumptions can influence an estimated response proportion.

The primary population is the full analysis set, described as all subjects from the randomized set to whom study treatment was assigned. That statement defines the intended analysis population at a high level. The registry record does not report a detailed participant flow, the number excluded from the endpoint analysis, or a separate account of analysis populations for every secondary outcome. These omissions limit assessment of how completely the analysis followed the randomized assignment and how missingness was handled beyond the stated primary-endpoint method.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: iridocyclitis (1.4%), abdominal hernia (1.4%), abdominal pain (1.4%), inguinal hernia (1.4%), erysipelas (1.4%).

The registry reports serious adverse events and other adverse events separately for treatment periods and groups. In Treatment Period 1, the serious-event figures are 4 of 71 at risk in the delayed NSAID-tapering secukinumab group, 3 of 70 in the early NSAID-tapering secukinumab group, and 1 of 70 in the placebo group. The listed other-adverse-event counts for those groups are 53 of 71, 56 of 70, and 55 of 70, respectively. The registry reports 0 deaths in each of these groups.

For Treatment Period 2, the serious-event figures are 1 of 71, 0 of 70, and 1 of 70 for the delayed-tapering, early-tapering, and placebo groups, respectively. Other-adverse-event counts are 25 of 71, 23 of 70, and 22 of 70. The registry reports 0 deaths in each group in this period. These are period-specific figures and should not be added together to create a participant total; the record does not establish whether the same participant could contribute to more than one period’s reporting.

The listed serious adverse-event terms are iridocyclitis, abdominal hernia, abdominal pain, inguinal hernia, erysipelas, and colitis, each reported as 1.4%. These safety counts describe events recorded in the registry; they do not establish causation or permit a complete comparative safety assessment. Further detail on event timing, severity beyond the serious classification, and participant-level overlap is not reported in the registry record.

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

The posted primary results describe a higher observed ASAS20 response proportion in the pooled secukinumab group than in the placebo group. The re-calculated risk difference is 0.068, but its 95% confidence interval ranges from -0.075 to 0.210. The sponsor’s logistic-regression result also has a 95% confidence interval that includes the value representing no odds difference. The estimates therefore remain uncertain and do not establish a precise treatment contrast.

The result does not show how much NSAID treatment was reduced for individual participants. The study included NSAID-related outcomes, including mean change in ASAS-NSAID score, but a group-level score change is not the same as a direct account of each participant’s tapering. The registry record does not provide a full description of the NSAID-sparing result beyond the listed outcomes and posted summaries.

The primary endpoint is a composite response classification. It does not show the separate contribution of each ASAS domain, and the pooled comparison does not distinguish the early from the delayed NSAID-tapering schedule. The endpoint also does not, by itself, determine whether an observed contrast is clinically important. The registry record does not report a threshold for clinical importance.

These results apply to the analysis and population described in the registry, including the full analysis set and non-responder imputation for missing primary data. They should not be extended automatically to other populations, treatment schedules, or follow-up periods. The primary comparison was at Week 12, and the registry’s summary does not establish outcomes beyond the reported time frames. Statistical uncertainty, missing-data assumptions, multiplicity, and incomplete reporting of the original analysis plan all remain relevant when interpreting what the results mean.

18. Why This Trial Matters Statistically

This trial raises several useful statistical questions for clinical researchers. First, its primary endpoint is a binary composite response, while the study’s broader purpose also concerns NSAID reduction. Those are related but distinct questions: a response proportion and a change in an NSAID-related score do not measure the same thing. Keeping the endpoint and the underlying clinical question aligned is essential to interpretation.

Second, the primary comparison pools two secukinumab groups that differ in NSAID-tapering timing. Pooling yields a single primary contrast against placebo, but it does not estimate the separate contribution of each tapering schedule. The secondary results include schedule-specific comparisons, which have their own uncertainty and multiplicity concerns.

Third, the reported estimate depends on its statistical scale. The sponsor reports an odds ratio from logistic regression, while the straightforward re-calculation reports a risk difference. Both can be informative, but they answer the comparison using different measures. Confidence intervals make clear that the point estimates should not be read without considering uncertainty.

Finally, the registry illustrates the importance of transparent reporting. The record specifies the primary outcome definition and missing-data method, but does not report the full statistical plan, multiplicity strategy, or original sample-size justification. Such details help readers distinguish planned confirmatory analyses from exploratory ones and assess how well the posted results answer the trial’s intended questions.

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 leaves several trial-specific interpretive details unreported. The original sample-size justification and its assumptions are not reported, so the completed study’s design rationale cannot be compared with the planning illustrations. The registry also does not report the full statistical analysis plan, including detailed model specifications, covariate handling, or a multiplicity strategy.

The primary comparison pools the two secukinumab schedules. That answers the stated pooled comparison but does not isolate the effect of early versus delayed NSAID tapering. The study’s secondary comparisons address some schedule-specific questions, but their interpretation is constrained by uncertainty and the unreported multiplicity approach.

The primary analysis used non-responder imputation for missing response data, but the registry does not report the number of missing observations, their reasons, or sensitivity analyses under alternative assumptions. The full analysis set is described, but a detailed participant flow and the analysis population for every secondary outcome are not reported in the registry record.

The primary endpoint is limited to a Week 12 response classification and does not provide domain-specific results in the primary summary. The record lists NSAID-related and other secondary outcomes, but not all details needed to assess their place in a prespecified hierarchy. The delayed-tapering arm description is truncated in the registry record, limiting interpretation of its full tapering procedure. Safety results are divided by treatment period, and participant overlap between periods is not reported. These limitations make the registry summaries informative but incomplete for reconstructing every design and analysis decision.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Examine the Clinical Efficacy and the Nonsteroidal Anti-inflammatory Drug (NSAID)-Sparing Effect of Secukinumab Over 16 Weeks in Patients With Ankylosing Spondylitis — NCT02763046.
• Registry record last updated 2021-10-08; status last verified 2021-10.
• Results first posted 2020-10-09.
• 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

NCT02763046 is a completed, randomized, triple-masked, parallel-group Phase 4 study of secukinumab in patients with ankylosing spondylitis. The registry lists enrollment as 211 and describes a placebo-controlled comparison that included early and delayed NSAID-tapering secukinumab groups. The primary endpoint was the Week 12 ASAS20 response in the pooled secukinumab group compared with placebo.

The posted primary counts were 72 of 141 for pooled secukinumab and 31 of 70 for placebo. The registry’s logistic-regression analysis reported an odds ratio of 1.32, with a 95% confidence interval from 0.74 to 2.36 and p = 0.351. The unadjusted risk-difference re-calculation is 0.068, with a 95% confidence interval from -0.075 to 0.210. Both intervals include values consistent with no difference.

The registry also records secondary outcomes related to NSAID use, disease activity, and quality of life, along with period-specific safety counts. The original sample-size justification, detailed statistical plan, and multiplicity strategy are not reported in the registry record.