Tocilizumab for Patients With Giant Cell Arteritis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tocilizumab for Patients With Giant Cell Arteritis (NCT01450137), a randomized phase 2 study. The primary outcome is Number of Patients That Have Achieved Complete Remission of Disease.

2. Clinical Question

This comparison concerns the added treatment contrast between tocilizumab and placebo in the context of glucocorticoid treatment. It is not a comparison of glucocorticoids against no glucocorticoids. The trial record identifies giant cell arteritis as the condition and describes the primary endpoint as complete disease remission after treatment. The registry record does not further define the clinical criteria used to determine complete remission, nor does it state how remission was adjudicated.

The registry also lists relapse-free status, cumulative glucocorticoid dose, and restricted mean survival time to first relapse after induction of remission among the secondary outcomes. The posted numerical secondary results include relapse-free participants at 12 months. Numerical results for cumulative glucocorticoid dose and restricted mean survival time are not reported in the registry record. These outcomes address related but distinct questions: remission at the specified primary time point, subsequent relapse experience, treatment exposure, and time until relapse.

3. Trial Design

This was a Phase II, randomized, parallel-group, placebo-controlled study of tocilizumab in patients with giant cell arteritis. The registry lists quadruple masking and an intended enrollment of 30. The completed study reports 30 participants, with 20 assigned to tocilizumab and 10 to placebo. The record gives the study start as 2011-09, primary completion as 2014-12, and status as completed.

Both arms received glucocorticoids in a standardized form. The tocilizumab arm is described as receiving tocilizumab 8mg/kg every 4 weeks until week 52; the comparator arm received placebo every 4 weeks until week 52. The primary endpoint was assessed at 12 weeks, while the relapse-free secondary outcome was assessed at 12 months. Thus, the primary endpoint and the later relapse outcome concern different follow-up points.

Randomization and masking can reduce some forms of systematic bias, but the registry record does not report the randomization sequence method, allocation concealment details, or which roles were included in quadruple masking. It also does not report the rationale for the unequal group sizes. The original sample-size assumptions and design justification are not reported in the registry record. The planning illustrations based on the observed effect are separate from the trial’s original design.

The stated primary population is all randomized patients, intention-to-treat. The record does not explain how missing primary outcomes were handled, whether every randomized participant contributed an observed outcome, or how participants were treated in the analysis if they did not complete follow-up. The registry gives a sponsor-reported Fisher Exact analysis of the risk difference for the primary endpoint. It does not report a fuller statistical analysis plan, including any prespecified covariate adjustment or interim analysis procedures.

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.

Up to Week 12

Reasons for not completing this period:

Week 12 to Study End

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized patients, intention-to-treat

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 Number of Patients That Have Achieved Complete Remission of Disease, measured over 12 weeks.

The primary endpoint is the number of patients who achieved complete remission of disease at 12 weeks. The registry describes the measure as a count of participants and identifies the analysis population as all randomized patients, intention-to-treat. The result is expressed as the number achieving remission in each treatment group; the comparison uses the difference between the groups’ proportions.

A binary endpoint such as remission status gives each participant one of two outcome categories at the assessment time: remission achieved or not achieved. It provides a direct way to compare the frequency of the target outcome between randomized groups. In general, a prespecified time point makes the comparison interpretable because the outcome is assessed at a common stage of follow-up. The registry identifies 12 weeks as the primary endpoint timeframe.

The choice of complete remission addresses whether the disease state met the endpoint definition, rather than measuring a continuous change in symptoms or laboratory values. However, the registry record does not report the detailed criteria for complete remission, the process for confirming it, or whether assessors used a formal adjudication procedure. These details matter when readers assess how reproducible and objective the endpoint classification may be.

The use of an intention-to-treat population is intended to preserve the randomized comparison by keeping participants analyzed according to their randomized groups. How this was implemented in the presence of missing outcome data is not reported in the registry record.

7. Results Posted in the Registry

• Tocilizumab: 85.0% (17/20) versus 40.0% (4/10) on control; risk difference 45.0 percentage points (95% CI 10.8 to 79.2), risk ratio 2.12 (0.97–4.64); unadjusted two-proportion z-test p = 0.011.

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 Relapse Free Patients

• 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:
  • Tocilizumab: 85.0% (17/20) versus 20.0% (2/10) on control; risk difference 65.0 percentage points (95% CI 35.7 to 94.3), risk ratio 4.25 (1.21–14.88); 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 Tocilizumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results have a direction consistent with the primary result: the relapse-free outcome at 12 months also favors the tocilizumab group in the observed counts. This is a related outcome, but it concerns status at a later time and is not the same endpoint as complete remission at 12 weeks. It adds information about subsequent relapse experience without serving as a substitute for the primary comparison.

The registry lists cumulative glucocorticoid dose and restricted mean survival time to first relapse after induction of remission as additional secondary outcomes. Numerical results for these outcomes are not reported in the registry record. As a result, the broader secondary-outcome pattern cannot be fully assessed from the posted numerical results. The listed outcomes cover different aspects of disease course and treatment exposure, so a complete interpretation would require the corresponding estimates and their uncertainty.

Secondary analyses usually carry less confirmatory weight than a prespecified primary analysis, particularly when several outcomes are examined. General statistical explanation: testing multiple outcomes creates more opportunities for apparently notable results to arise by chance, unless the analysis plan accounts for multiplicity. The registry record does not report a multiplicity adjustment or a hierarchical testing plan. The unadjusted secondary p-value should therefore be viewed as supportive and exploratory rather than as equivalent evidence to a single primary endpoint test.

The small number of participants also limits precision for the secondary comparison. The observed direction can be described, but the available record does not establish that every secondary measure would show a consistent effect. In particular, absent numerical results for two listed secondary outcomes, conclusions about glucocorticoid exposure or time to relapse are not reported in the registry record.

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

• Number of Relapse Free Patients
• Cumulative Dose of GCs in mg/kg
• Restricted Mean Survival Time to First Relapse After Induction of Remission

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

A risk difference is the difference between the proportion with an outcome in one group and the proportion with that outcome in the comparison group. Here, the outcome is complete remission by 12 weeks, and the reported estimate is 0.45. A positive value means that the observed proportion was higher in the tocilizumab group than in the placebo group. This is an absolute contrast on the probability scale, not a relative measure such as a risk ratio.

The estimate is based on the observed participant counts: 17 of 20 in the tocilizumab group and 4 of 10 in the placebo group. With a binary endpoint, the denominator in each arm matters as much as the number meeting the endpoint. The unequal group sizes also mean that the raw counts alone should not be compared without considering their respective group totals.

What does Fisher Exact test do?

Fisher Exact is a method for testing association between two categorical variables, here randomized group and remission status. It evaluates how compatible the observed distribution of outcomes is with a null hypothesis of no association, under the method’s assumptions. It is often used with small group counts because it calculates an exact probability under that framework rather than relying on a large-sample approximation. A p-value does not measure the size of the effect, the probability the null hypothesis is true, or the probability that the result will replicate.

The sponsor’s reported primary analysis is identified as Fisher Exact and reports a risk difference of 0.45, a 95% confidence interval from 0.11 to 0.79, and p = 0.030. The separate unadjusted recalculation reports p = 0.011. The registry record does not report enough analytic detail to explain why those p-values differ. The sponsor’s stated analysis and the simple recalculation should therefore be read as distinct statistical outputs, not combined into a single test result.

How should the confidence interval be read?

A confidence interval expresses uncertainty about an estimated quantity under a specified statistical procedure. The reported 95% interval for the primary risk difference runs from 0.11 to 0.79. Its lower and upper limits give a range of values compatible with the data and method at the stated confidence level. It does not mean that 95% of individual participants’ outcomes lie in that range, nor does it assign a 95% probability to the particular interval containing the fixed true effect.

The interval is wide enough to show that the magnitude of the difference is not estimated precisely. The positive lower limit is consistent with a positive difference under the reported interval procedure, while the distance between the limits reflects considerable uncertainty about how large that difference may be. Confidence intervals and p-values answer related but different questions: the interval conveys a range of effect estimates, while the p-value measures compatibility with a null model under a test.

Why do small samples and over-dispersion matter?

General statistical explanation: with few participants, each observed outcome has a relatively large influence on a group proportion. Estimates can consequently vary substantially from one sample to another, and confidence intervals may remain broad. Exact methods can be useful in this setting, but they do not create additional information or remove uncertainty arising from limited enrollment.

Over-dispersion is a general concern when observed variability exceeds what a model assumes. It can make standard errors too small if the model does not account for that extra variation. Over-dispersion is most directly relevant to outcomes modeled as counts or rates; the primary endpoint is binary and the sponsor analysis is reported as Fisher Exact. The registry record does not report a model-based over-dispersion assessment, and no such adjustment should be inferred for the primary result.

What does intention-to-treat mean?

In general, an intention-to-treat analysis retains participants in the groups to which they were randomized, regardless of subsequent treatment adherence. This supports the randomized comparison. The registry identifies all randomized patients as the primary analysis population. It does not report the handling of missing 12-week outcome data or provide a participant-flow account in the posted results. The label alone therefore does not resolve how missing outcomes were incorporated.

These methods describe the reported contrast, but they do not answer every design question. The registry record does not report the original sample-size justification, interim analysis plan, detailed remission criteria, or a full statistical analysis plan. Such omissions limit assessment of how fully the posted analysis follows prespecified procedures.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.45, with a sponsor-reported 95% confidence interval from 0.11 to 0.79. The interval is entirely on the positive side of zero, but it spans a broad range of effect magnitudes. It supports a positive difference under the reported interval procedure while leaving substantial uncertainty about the size of that difference.

Precision depends partly on how much information the data contain. The primary comparison includes 20 participants in the tocilizumab group and 10 in the placebo group. With group sizes of this scale, individual outcomes can meaningfully affect the estimated proportions. The unequal allocation also contributes to the limited information available in the smaller arm. The interval is therefore more informative than the point estimate alone: it makes the uncertainty visible rather than implying that 0.45 is known exactly.

A confidence interval is not a prediction interval for outcomes in future participants and does not describe the range of individual treatment responses. It is also not a guarantee that the true difference lies within the reported limits. Its interpretation depends on the analysis method and assumptions used to construct it.

The registry also reports a separate unadjusted recalculation, but the sponsor’s confidence interval is the reported interval for the stated primary analysis. The record does not report further interval methods or sensitivity analyses. For the 12-month relapse-free outcome, the sponsor-reported 95% interval for the risk difference runs from 0.36 to 0.94; that secondary estimate is also based on small groups and should be interpreted with similar attention to uncertainty.

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 planning figures are participants per arm for the binary outcomes, not total events. They are illustrations based on the observed effect rather than the original design assumptions for the trial. The assumptions stated for these illustrations are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. The original design assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column gives the corresponding planning figure for a 90% chance. Higher target power generally requires more participants, all else equal. These are planning quantities, not a description of what happened in this trial.

For the primary remission outcome, planning for 100% of the observed effect gives 17 participants per arm for 80% power and 23 participants per arm for 90% power. Planning for 75% of the observed effect gives 33 and 44 participants per arm, respectively. Planning for 50% of the observed effect gives 77 and 102 participants per arm, respectively. The pattern illustrates that smaller effects are harder to detect and require more participants under the stated assumptions.

These figures are not observed power. They should not be used to judge the completed trial by asking whether its enrollment matched a calculation based on the observed effect. An original design calculation would need the trial’s prespecified assumptions, which 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 = 0.400; treatment proportion p₁ = 0.850; average p̄ = 0.625.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6847 = 1.3419.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6062 = 0.5102.
4. n = (1.3419 + 0.5102)² / (0.4500)² = 16.9, rounded up to 17 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 <- 0.4                          # control proportion
p1 <- 0.85                          # 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(1450137)
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 = 17 (80% power), 23 (90% power)
 75% of observed effect: n per arm = 33 (80% power), 44 (90% power)
 50% of observed effect: n per arm = 77 (80% power), 102 (90% power)
power.prop.test: 16.9 
Simulated power at n = 17 per arm: 0.812 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s primary reported analysis uses Fisher Exact and gives a risk difference of 0.45, with a 95% confidence interval from 0.11 to 0.79 and p = 0.030. A separate simple, unadjusted recalculation from the posted summary counts reports the same risk-difference estimate and p = 0.011. The recalculation is not a replacement for the sponsor’s analysis; it is a distinct calculation based on the posted counts.

The p-values differ, while the reported risk-difference estimate is the same. The registry record does not describe enough detail to identify the reason for the difference. In particular, it does not provide a fuller analysis specification or additional information about how the reported test result was obtained. The difference should be noted rather than explained by an assumption about an unreported procedure.

Both outputs concern the same primary remission comparison and should be interpreted alongside the group counts and the confidence interval. The sponsor’s result is the analysis reported in the registry; the recalculation is useful as an independent unadjusted check of the posted summary statistics. Neither p-value indicates the probability that the treatment effect is real, and neither removes the uncertainty reflected by the confidence interval.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome is clearly identified as complete remission at 12 weeks, and the registry reports a sponsor analysis for that outcome. The record also lists several secondary outcomes, including relapse-free participants, cumulative glucocorticoid dose, and restricted mean survival time to first relapse. It does not report a multiplicity adjustment, a hierarchy for testing the outcomes, or a plan for controlling the overall false-positive rate across analyses. Without those details, the secondary p-values should not be interpreted as if each were the sole prespecified test.

Missing outcome handling is another important part of an intention-to-treat analysis. The registry identifies all randomized patients as the primary population, but does not report the number of participants with missing 12-week remission status, the imputation method, or any sensitivity analysis for missing data. It also does not describe whether participants who discontinued treatment or missed a visit were classified in a particular way. Those details are not reported in the registry record.

The analysis population label is useful because it indicates an intention to retain randomized allocation as the basis for comparison. However, the label cannot by itself show whether all randomized participants contributed an observed endpoint or how missing information affected the estimate. The outcome counts and arm totals are reported, but the record does not provide a participant-level flow or enough detail to reconcile all analysis decisions.

Likewise, the registry record does not report an interim analysis plan, stopping boundaries, or a detailed statistical analysis plan. It does not report whether any covariate adjustment was planned or performed. These omissions do not establish that the procedures were absent; they mean that their presence and implementation cannot be assessed from the registry record.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiovascular disease (20.0%), glucocorticoid related hyperglycaemia and myopathia (20.0%), gastrointestinal disease (15.0%), osteoporotic fracture (10.0%), back pain (10.0%).

Among participants in the tocilizumab group, 7 of 20 were reported as having a serious adverse event; in the placebo group, 5 of 10 were reported as having a serious adverse event. Other adverse events were reported for 11 of 20 participants in the tocilizumab group and 6 of 10 in the placebo group. The registry records 0 deaths in the tocilizumab group and 1 in the placebo group.

The listed serious adverse event terms include cardiovascular disease, glucocorticoid related hyperglycaemia and myopathia, gastrointestinal disease, osteoporotic fracture, back pain, and infectious disease. The registry reports percentages for these terms, but does not state the denominator or provide enough detail to establish how events were counted if a participant had more than one event. The percentages should not be interpreted as comparative risks without that context.

These figures are descriptive counts from groups of different sizes. They do not by themselves establish a treatment-related cause or provide a precise comparison of safety. The registry record does not provide detailed event timing, severity grading, attribution, or a full adverse-event listing. The small number of participants and the limited detail constrain what can be concluded from the posted safety information.

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

The posted primary results show a higher observed proportion achieving complete remission at 12 weeks in the tocilizumab group than in the placebo group, with both groups receiving standardized glucocorticoids. The estimated risk difference is 0.45, and the sponsor-reported 95% confidence interval extends from 0.11 to 0.79. This describes the observed randomized comparison and its uncertainty in this trial.

The result does not establish the exact size of an effect in other patients or settings. The small enrollment and broad confidence interval leave substantial uncertainty about magnitude. The study is Phase II, and the registry record does not report enough detail about participant characteristics, remission criteria, or missing data handling to assess all aspects of applicability and measurement.

The result is not evidence about tocilizumab without glucocorticoids. Both randomized groups received glucocorticoids, and the contrast is tocilizumab plus glucocorticoids versus placebo plus glucocorticoids. Although glucocorticoid dose is listed as a secondary outcome, its numerical result is not reported in the registry record. The primary remission result therefore does not demonstrate a reduction in glucocorticoid dose or duration.

The later relapse-free result is directionally consistent with the primary finding, but secondary outcomes have less confirmatory weight when multiplicity procedures are not reported. Numerical results for two other listed secondary measures are also not reported. Safety counts are available, but their level of detail and the small group sizes do not support a comprehensive assessment of comparative safety.

Statistical evidence from this trial is one part of an evidence base, not a substitute for evaluating study design, precision, safety, and findings from other studies. No conclusion about treatment advice follows from these registry results alone.

18. Why This Trial Matters Statistically

This trial illustrates several core issues in interpreting clinical data. A randomized comparison can make the treatment contrast clearer, but small group sizes still leave estimates vulnerable to sampling variation. The primary result has a positive estimated risk difference, yet its confidence interval spans a broad range. Reporting both the estimate and interval gives a more complete account than relying on a p-value alone.

The record also makes the distinction between an endpoint and the broader treatment rationale visible. The primary endpoint is remission at 12 weeks, whereas the stated rationale concerns reducing glucocorticoid dose and duration and achieving more durable remissions. The registry lists outcomes relevant to those questions, but numerical results for cumulative glucocorticoid dose and time to first relapse are not reported. A favorable result on one outcome cannot fill in missing evidence on another.

Comparisons between a sponsor-reported analysis and a simple recalculation are useful for understanding what can and cannot be verified from summary data. Here, the risk-difference estimate is the same, while the reported and recalculated p-values differ. The registry record does not explain the difference, emphasizing why full analysis details matter when results are registered.

Finally, secondary outcomes and safety counts require careful weighting. Several endpoints can broaden scientific understanding, but unadjusted secondary tests do not have the same confirmatory status as a designated primary outcome. Small safety counts are descriptive rather than definitive. Together, these considerations show why effect size, precision, analysis transparency, and completeness of reporting need to be read alongside statistical significance.

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 enrollment was 30, with 20 participants in the tocilizumab arm and 10 in the placebo arm. These small, unequal groups limit the precision of estimates and make the observed proportions sensitive to a small number of outcome classifications. The primary confidence interval is correspondingly broad, so the magnitude of the observed difference remains uncertain.

The registry record does not report the original sample-size justification, detailed remission criteria, missing-data procedures, or a full statistical analysis plan. It also does not report whether interim analyses were planned or whether any outcomes were subject to a prespecified multiplicity strategy. These gaps make it difficult to assess the extent to which the posted analysis followed planned procedures.

Only limited numerical secondary results are posted. The 12-month relapse-free result is available, but numerical findings for cumulative glucocorticoid dose and restricted mean survival time to first relapse are not reported in the registry record. This prevents a fuller assessment of the stated goals related to glucocorticoid exposure and durability of remission.

Safety information is also limited. Counts of participants with serious and other adverse events and deaths are reported, together with selected serious-event terms, but event-level detail, timing, attribution, and the denominator for the listed percentages are not reported. The registry record does not provide enough information to make a detailed comparative safety assessment.

Finally, the primary assessment occurs at 12 weeks while the treatment descriptions extend to week 52. The registry results alone do not show how outcomes evolved throughout the entire treatment period. These reporting and precision limitations should be considered when interpreting the observed findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Tocilizumab for Patients With Giant Cell Arteritis — NCT01450137.
• Registry record last updated 2019-02-12; status last verified 2018-09.
• Results first posted 2019-02-12.
• 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

NCT01450137 is a completed, randomized, quadruple-masked, parallel-group Phase II study of tocilizumab plus glucocorticoids versus placebo plus glucocorticoids in giant cell arteritis. The record reports 30 participants, with 20 assigned to tocilizumab and 10 to placebo. The primary endpoint was complete remission at 12 weeks in all randomized patients, intention-to-treat.

The sponsor-reported risk difference was 0.45, with a 95% confidence interval from 0.11 to 0.79. The sponsor reported a Fisher Exact p-value of 0.030; an unadjusted recalculation reports p = 0.011. Relapse-free status at 12 months is also reported, while numerical results for cumulative glucocorticoid dose and restricted mean survival time to first relapse are not reported in the registry record.

The enrollment, unequal group sizes, broad primary confidence interval, unreported design and missing-data details, and limited safety information are important context for interpreting the findings.