Infliximab Plus Intravenous Immunoglobulin for the Primary Treatment of Kawasaki Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Infliximab Plus Intravenous Immunoglobulin for the Primary Treatment of Kawasaki Disease (NCT00760435), a randomized phase 3 study. The primary outcome is The Number of Subjects in Each Arm That Have Persistent or Recrudescent Fever 24 Hours After Completion of the Intravenous Immunoglobulin (IVIG) Infusion.

2. Clinical Question

The trial addressed whether adding infliximab to primary treatment for acute Kawasaki disease would reduce persistent or recrudescent fever after IVIG. The registry describes the standard primary therapy as IVIG and high-dose aspirin; the named arms are infliximab plus IVIG and placebo plus IVIG. The central comparison is therefore the addition of infliximab against a placebo comparison alongside IVIG.

3. Trial Design

This was a phase 3, randomized, quadruple-masked, parallel-group trial. The registry lists enrollment as 196 and status as completed. The trial began in 2009-03, with primary completion in 2012-10. The sponsor was the University of California, San Diego.

The two named arms were infliximab plus IVIG and placebo plus IVIG. The study purpose was to determine whether adding infliximab to standard primary therapy of IVIG and high-dose aspirin would reduce resistance to therapy in acute Kawasaki disease. The registry's arm descriptions specify IVIG in both groups; additional details about treatment administration are not reported in the registry record.

The primary outcome was the number of participants in each arm with persistent or recrudescent fever 24 hours after completion of IVIG. Its stated timeframe was 10 weeks. The posted comparison uses 98 participants in the infliximab arm and 97 in the placebo arm. The outcome description notes that one placebo-group subject was removed from the modified intention-to-treat analysis because the subject left the study before receiving placebo.

Randomization and masking describe important features of the design, but details such as the randomization procedure, allocation concealment, and which parties were masked are not reported in the registry record. The record lists three secondary outcomes: fever days during the study period, change in C-reactive protein at 24 hours after IVIG, and change in left anterior descending coronary artery outcomes at week 2.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: 1 subject in the placebo group was removed from the modified ITT analysis (this subject was removed from the study prior to receiving the placebo)

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 The Number of Subjects in Each Arm That Have Persistent or Recrudescent Fever 24 Hours After Completion of the Intravenous Immunoglobulin (IVIG) Infusion, measured over 10 weeks.

The primary endpoint counts participants with persistent or recrudescent fever 24 hours after completion of the IVIG infusion. Persistent fever refers to fever continuing after treatment; recrudescent fever refers to fever returning after it has subsided. The registry combines these into one binary outcome: each participant either met the fever outcome or did not. The reported measure is the number of participants in each arm who had the outcome.

This endpoint was chosen to address the study’s stated question about resistance to primary therapy. Fever after IVIG provides an observable clinical event for comparing the treatment groups. The registry names the outcome as the number in each arm and gives a 10 weeks timeframe, while specifying the fever assessment at 24 hours after IVIG completion. Further details about fever definitions, measurement schedules, or adjudication are not reported in the registry record.

The posted primary counts were 11 participants in the infliximab arm and 11 in the placebo arm. The comparison analysis uses 98 participants for infliximab and 97 for placebo. The outcome description notes that one placebo-group subject was excluded from the modified intention-to-treat analysis after leaving before receiving placebo. This count-based endpoint is distinct from the secondary outcomes, which include fever days, a laboratory measure, and a coronary artery measure.

7. Results Posted in the Registry

• Infliximab: 11.2% (11/98) versus 11.3% (11/97) on control; risk difference -0.1 percentage points (95% CI -9.0 to 8.8), risk ratio 0.99 (0.45–2.17); unadjusted two-proportion z-test p = 0.980.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: participants are counted according to whether persistent or recrudescent fever occurred. For a binary endpoint, the analysis can compare the proportion with the event in each arm, as well as express the contrast on relative scales. The posted result includes a risk difference, risk ratio, and odds ratio. These measures answer related but distinct questions about how the event frequency compares between groups.

What does the risk difference express?

The risk difference subtracts the event risk in the placebo group from the event risk in the infliximab group. A value at the null corresponds to equal event risks; a negative estimate points toward a lower observed event risk in the infliximab group, and a positive estimate points toward a higher one. The posted estimate is close to zero. Its confidence interval runs from -0.09 to 0.088, so it includes the null and extends to values on either side. The result therefore does not identify a precise direction or size of difference.

How do ratios differ from a risk difference?

A risk ratio compares event risks by division, while an odds ratio compares event odds. For either ratio, the null is the value representing equal groups. The posted risk ratio is 0.990, with a confidence interval from 0.451 to 2.175; the posted odds ratio is 0.989, with a confidence interval from 0.407 to 2.401. Both intervals span their null value. Ratios can look different from absolute differences because they use a different scale; they should be interpreted with the event counts and uncertainty in view.

What does the p-value contribute?

The reported unadjusted p-value is 0.98. In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. A large p-value does not show that the null is true, and it is not a measure of the probability that treatment effects are equal. It also does not describe the range of plausible effects; the confidence interval is more directly informative about precision.

The label “unadjusted” indicates that the posted p-value is not described as adjusted for multiplicity. Whether the sponsor’s analysis included other adjustments is not reported in the registry record. The trial’s statistical analysis plan, including model details, covariate adjustment, and planned testing procedures, is not reported in the registry record. The presented comparison should therefore be interpreted as the posted analysis, without assuming additional methods.

Why does the analysis population matter?

The primary outcome description identifies a modified intention-to-treat analysis and says one subject assigned to placebo was removed because that subject left before receiving placebo. The posted comparison uses 97 placebo participants and 98 infliximab participants. This exclusion is relevant because the analysis population determines which randomized participants contribute to the comparison. The registry does not report further details about other missing outcomes, deviations, or population definitions, so those cannot be evaluated from this record.

In general, random allocation aims to make treatment groups comparable at the start of a trial, while masking can reduce some forms of bias in treatment delivery and outcome assessment. The registry identifies the trial as randomized and quadruple-masked, but does not describe the allocation procedure or identify the masked roles. These design labels alone do not establish how successfully bias was controlled in practice.

Why can over-dispersion matter?

Over-dispersion is a general concern for count outcomes when observed variation is greater than a model expects. It can lead to uncertainty estimates that are too narrow if the model does not account for the extra variation. The primary endpoint is reported as the number of participants with a binary fever outcome, rather than as a recurrent-event count per participant. The registry does not report an over-dispersion model or other model diagnostics. The general concept is therefore useful background, not a claim that over-dispersion occurred in this analysis.

Because the event counts are the same in the two arms and the estimated difference is close to zero, the point estimate alone gives little evidence about precision. The interval is essential: it allows for effects in both directions and is broad relative to the near-zero estimate. The result is not a formal equivalence or non-inferiority conclusion, because the registry does not report a prespecified margin or corresponding analysis.

10. Confidence Intervals and Precision

The risk-difference estimate is close to zero, but its 95% confidence interval extends from -0.09 to 0.088. This interval includes the null value and reaches values on both sides of it. Thus, the posted result does not pin down the magnitude or direction of the difference with much precision. The equal count of 11 fever outcomes in each arm does not remove this uncertainty, particularly because the analysis includes 98 participants in the infliximab arm and 97 in the placebo arm.

The relative-effect intervals are also broad. The risk ratio is 0.990, with a confidence interval from 0.451 to 2.175; the odds ratio is 0.989, with a confidence interval from 0.407 to 2.401. Each interval spans its no-difference value. The estimates lie near that value, but the intervals are compatible with meaningfully different relative effects in either direction.

In general, confidence intervals show the range of estimates reasonably compatible with the data and the analysis assumptions; they are not guarantees that the true effect lies within a particular observed interval. The interval width reflects statistical uncertainty, not the importance of the outcome. These results do not establish equivalence, and the registry does not report a clinically acceptable equivalence or non-inferiority margin.

11. 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 table and curve give planning illustrations based on the observed effect, rather than the trial’s original design assumptions. These figures are participants per arm, not total events. The planning assumptions listed 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 planning figures are not observed power.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the listed assumptions, if that effect and the model assumptions were correct. The 90% power column gives the corresponding planning target for a 90% chance. These are design calculations, not a measure of the probability that the trial’s finding is true.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. As the effect targeted for detection becomes smaller, more participants are required to distinguish it from random variation under the same assumptions. The displayed values are very large because the observed effect is close to zero. They should be read as illustrations of the implications of planning around this estimate, not as enrollment recommendations or as evidence that the trial was designed to detect these particular effects.

The registry’s own sample-size justification and original design assumptions are not reported in the registry record. These calculations do not replace that missing information.

12. 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 = 0.113; treatment proportion p₁ = 0.112; average p̄ = 0.113.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4474 = 0.8769.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4474 = 0.3766.
4. n = (0.8769 + 0.3766)² / (-0.0012)² = 1,173,429.5, rounded up to 1,173,430 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 <- 0.11340206185567                          # control proportion
p1 <- 0.112244897959184                          # 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(760435)
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 = 1,173,430 (80% power), 1,570,889 (90% power)
 75% of observed effect: n per arm = 2,088,432 (80% power), 2,795,818 (90% power)
 50% of observed effect: n per arm = 4,704,223 (80% power), 6,297,619 (90% power)
power.prop.test: 1173430 
Simulated power at n = 1,173,430 per arm: 0.800 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists four outcome measures in total and identifies three secondary outcomes: days of fever following therapy during the study period, change in C-reactive protein from baseline at 24 hours after IVIG completion, and change from baseline in left anterior descending coronary artery outcomes at week 2. No secondary analyses are posted. The available comparative result is therefore the primary fever outcome; the listed secondary measures cannot be interpreted as having demonstrated any particular result.

When several outcomes or comparisons are tested, the chance of at least one apparently notable result can increase. Statistical methods can address this multiplicity, but the registry does not report a testing hierarchy, adjustment procedure, or multiplicity plan. The posted primary p-value is described as unadjusted. No assumption should be made that the secondary outcomes were tested, adjusted, or omitted according to a particular plan.

The primary outcome description notes that one placebo-group subject was excluded from the modified intention-to-treat analysis because the subject left the study before receiving placebo. The primary comparison denominators are 98 in the infliximab group and 97 in the placebo group. The registry does not report whether other participants had missing outcome measurements, how any such missingness was handled, or whether sensitivity analyses were performed.

The record does not give a fuller definition of the modified intention-to-treat population or identify other analysis populations. It also does not report the statistical analysis plan, prespecified handling of protocol deviations, or details of any interim analyses. These omissions limit evaluation of whether the posted analysis followed prespecified procedures and how robust it might be to alternative missing-data assumptions.

14. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fever (11.3%), coronary artery abnormality (6.1%), headache (2.0%), uri (2.0%), rash (1.0%).

The registry lists serious adverse events in 22 of 98 participants at risk in the infliximab arm and 17 of 98 participants at risk in the placebo arm. These are descriptive group counts. The record does not provide a comparative statistical analysis for serious adverse events, so the counts alone do not establish whether the groups differ in safety.

The listed serious adverse event terms include Fever at 11.3%, Coronary artery abnormality at 6.1%, Headache at 2.0%, URI at 2.0%, Rash at 1.0%, and Anemia at 1.0%. These percentages are presented as the leading serious terms in the registry; corresponding event counts by arm are not reported in the registry record. The record does not establish from this list whether participants could contribute more than one term.

The safety denominator for the placebo arm is 98, whereas the primary comparison denominator is 97. The primary outcome description explains an exclusion from its modified intention-to-treat analysis; the safety record does not explain the denominator difference. Death counts are not reported in the registry record. These safety entries should be read as posted adverse-event information, not as a complete assessment of risks or a basis for treatment advice.

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

The posted primary result is that 11 participants in the infliximab arm and 11 in the placebo arm had persistent or recrudescent fever. The estimated risk difference is close to zero, and its confidence interval crosses the null and extends in both directions. The unadjusted p-value is 0.98. Together, these statistics show that the posted comparison does not provide a precise estimate of a difference between the groups.

This finding does not prove that the treatments are equivalent or that no effect exists. A non-significant result can arise when the data are compatible with a range of effects, and the confidence interval remains broad. Equivalence or non-inferiority requires a prespecified margin and an analysis designed to address that question; such a margin and analysis are not reported in the registry record.

The interpretation is specific to the posted fever endpoint, its stated assessment after IVIG, and the analysis population described in the registry. It does not establish results for fever days, C-reactive protein, or coronary artery outcomes, because no analyses for the three listed secondary outcomes are posted. Nor do the adverse-event counts provide a complete comparative safety assessment.

The trial is listed as randomized and quadruple-masked, which are features intended to support a fair comparison and reduce some biases. However, details of the implementation and the statistical analysis plan are not reported in the registry record. The results therefore describe the posted evidence, with its stated denominators and uncertainty, rather than a definitive answer about treatment effects.

16. Why This Trial Matters Statistically

This trial illustrates why an observed group contrast and its uncertainty should be read together. The fever counts are identical across the two arms, and the risk-difference estimate is near zero. Yet the confidence interval extends to values on either side of the null. The point estimate alone can make a comparison appear settled when the interval shows that the data do not precisely determine the effect.

It also demonstrates the distinction between a test of a null hypothesis and a claim of equivalence. The unadjusted p-value is 0.98, but a large p-value does not show that the treatments have the same effect. An equivalence conclusion would require a prespecified margin and an appropriate analysis, neither of which is reported in the registry record.

The record further illustrates that endpoint counts, analysis denominators, and safety denominators need to be kept distinct. The primary comparison includes 98 infliximab participants and 97 placebo participants, while the safety groups list 98 participants at risk in both arms. The stated exclusion from the modified intention-to-treat analysis helps explain the primary denominator, but the reason for the safety denominator difference is not reported.

Finally, the planning illustration makes the observed effect’s scale consequential for future design calculations. Because the observed effect is close to zero, the corresponding participant-per-arm figures are very large, and smaller target effects require more participants under the stated assumptions. That illustration is not a substitute for a trial-specific sample-size justification, which is not reported in the registry record.

17. Limitations

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

The registry record does not report detailed eligibility criteria, the randomization procedure, allocation concealment, or the identities of the parties included in quadruple masking. These details would help readers assess how the trial was implemented, but they cannot be inferred from the design labels alone.

The primary outcome description gives the fever assessment point and a 10 weeks timeframe, but does not provide a detailed operational definition of persistent or recrudescent fever, measurement procedures, or adjudication methods. The posted primary comparison is based on a modified intention-to-treat population, with one placebo-group subject excluded before receiving placebo. Additional missing-data information and sensitivity analyses are not reported in the registry record.

The registry lists three secondary outcomes but posts no secondary analyses. It also does not report a statistical analysis plan, multiplicity procedures, a sample-size justification, or details of interim analyses. The planning figures are illustrations based on the observed effect and listed assumptions, not evidence about the original design rationale.

Safety denominators differ from the primary outcome denominators: both safety groups list 98 participants at risk, while the primary comparison uses 97 placebo participants and 98 infliximab participants. The registry does not explain this difference. Death counts are not reported in the registry record, and the serious adverse event terms are not accompanied by arm-specific counts. These limitations constrain how fully the posted efficacy and safety information can be assessed.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Infliximab Plus Intravenous Immunoglobulin for the Primary Treatment of Kawasaki Disease — NCT00760435.
• Registry record last updated 2014-11-24; status last verified 2014-11.
• Results first posted 2014-11-13.
• 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.

21. Record Summary

The registry record describes a completed, randomized, quadruple-masked, parallel-group phase 3 trial sponsored by the University of California, San Diego. Enrollment was 196. The study compared infliximab plus IVIG with placebo plus IVIG for primary treatment of acute Kawasaki disease.

The primary outcome was the number of participants with persistent or recrudescent fever 24 hours after IVIG completion, with a stated timeframe of 10 weeks. The posted counts were 11 in each arm; the comparison used 98 infliximab participants and 97 placebo participants. The risk-difference estimate was close to zero, with a confidence interval spanning the null, and the unadjusted p-value was 0.98.

Three secondary outcomes are listed, but no secondary analyses are posted. The registry also reports serious adverse event counts and leading serious event terms. Important details about the analysis plan, missing data, multiplicity, and original sample-size justification are not reported in the registry record.