A Study of the Safety and Efficacy of CNTO 148 (Golimumab) in Children With Juvenile Idiopathic Arthritis (JIA) and Multiple Joint Involvement Who Have Poor Response to Methotrexate (GO KIDS): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Safety and Efficacy of CNTO 148 (Golimumab) in Children With Juvenile Idiopathic Arthritis (JIA) and Multiple Joint Involvement Who Have Poor Response to Methotrexate (GO KIDS) (NCT01230827), a randomized phase 3 study. The primary outcome is Percentage of Participants With American College of Rheumatology (ACR) 30 Response at Week 16 Who Did Not Experienced a Flare of Disease Through Week 48.

2. Clinical Question

3. Trial Design

The registry describes a Phase 3, randomized, parallel-group, triple-masked, multicenter, double-blind randomized-withdrawal trial. It evaluated subcutaneous golimumab in participants with active polyarticular juvenile idiopathic arthritis despite standard therapy. The registry lists an enrollment of 173 and a status of terminated. The start is recorded as 2010-12 and primary completion as 2013-09. The reason for termination is not reported in the registry record.

The design first exposed participants to golimumab. The arm descriptions state that all participants received golimumab 30 mg per square meter every 4 weeks from Week 0 through Week 12. Participants with a clinical response at Week 16 were randomized to continue golimumab or receive placebo through Week 48. The available arm-description text is truncated, so further details of treatment changes or other study procedures are not reported in the registry record.

This design asks a conditional question: among people who initially responded to golimumab, what happened after random assignment to continue treatment or switch to placebo? It does not directly compare starting golimumab with starting placebo in all enrolled participants. The primary population is described as participants who achieved ACR Ped 30 response and were randomized at Week 16. The randomized groups contained 76 participants assigned to placebo and 78 assigned to golimumab for the primary outcome.

The full protocol, the reason for termination, and details such as the original sample-size justification, planned interim analyses, and the trial's prespecified statistical plan are not reported in the registry record. Those omissions limit how completely the conduct and analysis can be assessed from the registry alone.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population included all participants achieving American College of Rheumatology (ACR) Pediatric (Ped) 30 response who were randomized at Week 16.

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 Percentage of Participants With American College of Rheumatology (ACR) 30 Response at Week 16 Who Did Not Experienced a Flare of Disease Through Week 48, measured over Week 16 through Week 48.

The primary endpoint is the percentage of Week 16 ACR Ped 30 responders who were randomized and did not experience a disease flare between Week 16 and Week 48. The registry defines flare as worsening from Week 16 by 30% or more in 3 of the 6 ACR Pediatric Core Set variables, with no more than 1 variable improving by more than 30% at the time of flare. The variables cover physician and participant or parent assessments, active joints, joints with limited range of motion, physical function measured by the childhood health assessment questionnaire, and erythrocyte sedimentation rate.

The endpoint focuses on maintenance of response after the randomized withdrawal decision. In general, measuring flare can capture loss of disease control over follow-up rather than a single assessment at the end of follow-up. The definition also makes clear that flare is a composite rule: it depends on changes across several clinical and laboratory measures, not on one measure alone.

The recorded calculation divides the number of participants who responded and did not experience flare by the number randomized. This denominator is important when interpreting the percentages: the reported primary result concerns the Week 16 responder group that entered randomization, not every participant originally enrolled. The registry does not report further detail about how missing endpoint assessments were handled.

7. Results Posted in the Registry

• CNTO 148 (Golimumab): 59.0% (46/78) versus 52.6% (40/76) on control; risk difference 6.3 percentage points (95% CI -9.3 to 22.0), risk ratio 1.12 (0.84–1.49); unadjusted two-proportion z-test p = 0.428.

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.

Percentage of Participants With American College of Rheumatology (ACR) 30 Response at Week 48

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CNTO 148 (Golimumab): 52.6% (41/78) versus 55.3% (42/76) on control; risk difference -2.7 percentage points (95% CI -18.4 to 13.0), risk ratio 0.95 (0.71–1.27); unadjusted two-proportion z-test p = 0.737.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CNTO 148 (Golimumab) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With American College of Rheumatology (ACR) 30 Response Who Had Inactive Disease at Week 48

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CNTO 148 (Golimumab): 39.7% (31/78) versus 27.6% (21/76) on control; risk difference 12.1 percentage points (95% CI -2.7 to 26.9), risk ratio 1.44 (0.91–2.27); unadjusted two-proportion z-test p = 0.112.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CNTO 148 (Golimumab) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Achieved Clinical Remission While on Medication for Juvenile Idiopathic Arthritis (JIA) at Week 48

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CNTO 148 (Golimumab): 12.8% (10/78) versus 11.8% (9/76) on control; risk difference 1.0 percentage points (95% CI -9.4 to 11.4), risk ratio 1.08 (0.47–2.52); unadjusted two-proportion z-test p = 0.854.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CNTO 148 (Golimumab) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover ACR 30 response at Week 48, inactive disease among participants with an ACR 30 response, and clinical remission while on medication at Week 48. Taken together, their point estimates do not form a uniformly aligned pattern in favor of one randomized group. The risk-difference confidence intervals include zero across these comparisons, leaving substantial uncertainty about the direction and size of each difference.

These outcomes add descriptive context to the primary result, but they do not provide an independent resolution of its uncertainty. The primary outcome concerns absence of flare among Week 16 responders through Week 48, while the secondary measures address different status or response definitions. Related outcomes can offer complementary information, but differences in definitions and populations matter when comparing their results.

The registry lists no reported analyses for the secondary outcomes and does not report a multiplicity adjustment. In general, testing several outcomes increases the opportunity for at least one apparently notable result to arise by chance. Unadjusted secondary results therefore carry less confirmatory weight than a prespecified primary comparison analyzed under a documented plan. They can be useful for generating questions, but should not be treated as definitive evidence on their own.

Interpretation is also limited by the absence of further analysis details, including how missing measurements were handled and whether the secondary populations exactly matched the primary randomized population. The posted results can describe the observed group percentages and uncertainty, but they cannot establish a coherent pattern beyond the limitations of the registry record.

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

• Percentage of Participants With American College of Rheumatology (ACR) 30 Response at Week 48
• Percentage of Participants With American College of Rheumatology (ACR) 30 Response Who Had Inactive Disease at Week 48
• Percentage of Participants Who Achieved Clinical Remission While on Medication for Juvenile Idiopathic Arthritis (JIA) at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the registry's definition of no flare through Week 48 or did not. The posted percentages are proportions of participants, and the comparison is expressed as a risk difference. In general, a risk difference subtracts the event proportion in one group from that in the comparison group. A value of zero corresponds to equal proportions; positive or negative values indicate which group has the higher proportion according to the stated comparison direction. The posted risk difference is 0.063, with the golimumab group listed as the comparison against placebo.

The primary endpoint is based on the Week 16-to-Week 48 period. The denominator is participants randomized at Week 16 after achieving an ACR Ped 30 response. This population definition is essential: the observed percentages do not describe everyone enrolled at the start. The registry identifies 76 participants in the placebo group and 78 in the golimumab group for this outcome. It reports 40 participants with the endpoint in the placebo group and 46 in the golimumab group.

What does the confidence interval represent?

A confidence interval expresses statistical uncertainty around an estimated effect. In general, it describes a range of effect values that are reasonably compatible with the observed data under the method used to construct the interval. It is not a guarantee that the true effect lies in that range, nor does it represent the range of outcomes for individual participants. For the primary risk difference, the interval runs from -0.093 to 0.22. Because zero lies within that range, the data do not sharply distinguish a positive difference from no difference or a difference in the opposite direction.

The registry does not report the method used to calculate the confidence interval. The posted comparison also includes an unadjusted p-value of 0.428. In general, a p-value measures how unusual data at least as inconsistent with a null hypothesis would be if that hypothesis and the test assumptions held. It does not measure the probability that the null hypothesis is true, and it does not show whether an effect is important in practice. The word “unadjusted” matters because the record does not show that the comparison accounts for other outcomes or multiple analyses.

Why is a randomized comparison useful?

Random assignment is intended to make the groups comparable on average with respect to factors that may influence the outcome. That can support a causal comparison within the randomized population, subject to the conduct of the trial, the analysis population, missing data, and other assumptions. In this study, random assignment occurred at Week 16 among participants who had already responded to golimumab. The resulting comparison is therefore specific to those responders and to the continuation-versus-withdrawal question.

The record describes the trial as triple-masked and the official title as double-blind. Masking is generally used to reduce the possibility that knowledge of treatment assignment influences participants, clinicians, or outcome assessment. The registry does not identify exactly which groups of people were included in the triple masking, so that detail should not be inferred.

How should the flare definition be understood?

The flare outcome is a rule based on change in multiple ACR Pediatric Core Set variables from Week 16. In general, a composite definition can capture different manifestations of worsening, but its meaning depends on the specified components and thresholds. Here, the registry requires worsening of 30% or more in 3 of 6 variables and restricts how many variables may improve by more than 30% at the time of flare. The rule includes physician and participant or parent global assessments, joint measures, physical function, and erythrocyte sedimentation rate. A participant could therefore meet the rule through different combinations of changes across those measures.

The registry does not report details about adjudication of flare, handling of assessments taken outside scheduled visits, or how missing component measurements affected classification. Those methodological details could affect interpretation of a composite endpoint but cannot be reconstructed from the posted record.

What can the posted analysis establish?

The registry lists no reported analyses. The numerical comparisons therefore give descriptive estimates and unadjusted statistical summaries, but the record does not document a full analysis plan or show whether additional prespecified methods were used. The original sample-size justification, any interim analyses, and an adjustment strategy for multiple endpoints are not reported in the registry record.

General statistical principles help explain why these omissions matter. Prespecified analyses reduce the risk that methods are selected after results are known. Multiplicity procedures can address the increased chance of a chance-positive finding when several outcomes are tested. Missing-data methods can affect estimates when outcome information is absent. None of these details should be assumed to have been used or not used beyond what the registry states.

The sample-size illustrations are separate from the observed trial analysis. They use the observed effect as a planning reference under stated assumptions; they are not observed power. In general, power is a design property describing the probability that a planned test will detect an effect of a specified size under the assumed model. It does not indicate the probability that the observed finding is true, and a retrospective calculation based on the observed effect cannot replace the trial's own design justification.

11. Confidence Intervals and Precision

The primary estimate is 0.063 for the risk difference, and its confidence interval extends from -0.093 to 0.22. The interval crosses zero, which means the posted data are compatible with no difference. It also spans values on both sides of zero, so the uncertainty includes possible effects favoring either group. The result should not be described as a precise estimate of the size or direction of a difference.

The confidence interval is wide enough that the point estimate alone would be an incomplete description. The point estimate is the best single summary under the reported calculation, but the interval indicates that substantially different effects remain compatible with the data. This is why a statement based only on which arm has the numerically larger percentage can overstate what the comparison establishes.

In general, interval width reflects both the amount of information and the variability in the data, along with the interval method. The randomized groups for the primary outcome contained 76 participants assigned to placebo and 78 assigned to golimumab. The registry does not report the confidence-interval method, missing-data assumptions, or a precision target used when planning the trial. Those omissions prevent a fuller assessment of why this interval has its particular width.

The secondary risk-difference intervals also include zero. Their estimates should likewise be interpreted with attention to uncertainty, rather than by ranking the point estimates or treating a numerical direction as decisive. Confidence intervals describe statistical precision under the method used; they do not capture every source of uncertainty, including limitations in the registry record or the possibility that the analysis differed from a prespecified plan.

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 illustrations describe hypothetical future planning based on fractions of the observed effect. The figures are participants per arm for 80% power and participants per arm for 90% power; they are not totals across both arms. The posted assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is the stated fraction of the observed effect. The original trial's design assumptions are not reported in the registry record.

The 80% power column gives the participants per arm estimated to be needed, under those assumptions, for an 80% chance of detecting the specified effect if that effect is real and the assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations, not guarantees: actual results depend on the true effect, outcome rates, analysis method, and other features of a future study.

Rows describe planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the planning requirement rises as the target effect becomes smaller. The numbers are illustrations rather than a reconstruction of the terminated trial's design, and they do not explain why its enrollment was selected.

This is not observed power. Observed power is not a useful substitute for reading the estimate and its confidence interval; the planning values instead show how sample requirements change under stated assumptions and candidate effect sizes.

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 = 0.526; treatment proportion p₁ = 0.590; average p̄ = 0.558.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7023 = 1.3765.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7009 = 0.5899.
4. n = (1.3765 + 0.5899)² / (0.0634)² = 961.2, rounded up to 962 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 <- 0.526315789473684                          # control proportion
p1 <- 0.58974358974359                          # 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(1230827)
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 = 962 (80% power), 1,287 (90% power)
 75% of observed effect: n per arm = 1,716 (80% power), 2,297 (90% power)
 50% of observed effect: n per arm = 3,873 (80% power), 5,185 (90% power)
power.prop.test: 961.2 
Simulated power at n = 962 per arm: 0.797 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary outcome and three secondary outcomes, but does not report an analysis plan or any reported analyses. It also does not state whether the trial used a prespecified hierarchy among outcomes, a multiplicity adjustment, or another method to control the chance of false-positive findings across comparisons. These details are not reported in the registry record and should not be inferred from the posted p-values.

In general, multiplicity arises when investigators evaluate multiple outcomes, time points, or comparisons. The more statistical questions considered, the greater the chance that at least one result may appear unusual by chance alone. Adjustment methods or a prespecified testing sequence can help manage that issue, but they can also affect how estimates and p-values are interpreted. Without a documented approach, unadjusted secondary comparisons warrant particular caution.

The primary population is described as the intent-to-treat population of participants who achieved ACR Ped 30 response and were randomized at Week 16. That is a defined subset of the enrolled participants, reflecting the randomized-withdrawal design. The registry does not report a separate analysis population for each secondary outcome or give a full account of how participants were included in each calculation.

Missing-data handling is not reported in the registry record. The available results do not specify how missing visits, incomplete flare assessments, withdrawal, or unavailable endpoint measurements were treated. In general, missing-data choices can influence a binary outcome estimate, especially if missingness is related to treatment assignment or health status. No particular imputation, censoring, or other approach can be assumed.

The original sample-size justification, planned interim analyses, and detailed statistical methods are also not reported. The posted planning illustrations are based on observed effects and stated calculation assumptions; they do not establish what assumptions or targets guided the original trial. Together, these gaps limit assessment of whether the posted analyses match a prespecified plan and how robust the results are to alternative analysis choices.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: juvenile idiopathic arthritis (10.5%), vertigo (10.0%), pain (10.0%), arthritis (10.0%), cellulitis (5.3%).

The registry reports serious adverse event counts for four groups, with the number at risk and the number affected listed separately. Group I, participants who did not enter the randomized-withdrawal period, had 4 serious adverse events among 19 at risk. Group II, placebo subcutaneously plus methotrexate, had 2 among 10. Group III, placebo plus methotrexate followed by golimumab 30 mg per square meter plus methotrexate, had 15 among 66. Group IV, golimumab plus methotrexate, had 18 among 78.

These group labels describe different treatment histories, and the registry record does not provide enough detail to treat them as a single randomized safety comparison. The counts should be read in relation to each group's listed number at risk, not as direct evidence that one treatment is safer than another. Exposure duration, event collection details, and adjusted safety comparisons are not reported in the registry record.

The listed serious adverse event terms include juvenile idiopathic arthritis at 10.5%, vertigo at 10.0%, pain at 10.0%, arthritis at 10.0%, cellulitis at 5.3%, and herpes zoster at 5.3%. The registry does not clarify the denominator for these listed percentages in the available record. Death counts are not reported in the registry record; that is not equivalent to evidence that no deaths occurred.

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

The primary result describes the proportion of Week 16 responders who were randomized and then did not experience a flare through Week 48. The posted percentages were 59.0% for golimumab and 52.6% for placebo, with an estimated risk difference of 0.063. The confidence interval from -0.093 to 0.22 includes zero, and the unadjusted p-value is 0.428. These statistics show a numerical difference in the observed groups but substantial uncertainty around its direction and size.

The result applies to the particular randomized-withdrawal question. Participants first received golimumab and only those with a Week 16 response were randomized. It therefore does not estimate what would happen if all eligible children started golimumab rather than placebo, nor does it characterize the participants who did not reach the responder randomization. It also should not be generalized automatically to people outside the trial population or to different treatment settings.

A confidence interval that includes zero does not prove that the groups are identical. Likewise, a numerical difference does not establish a treatment effect. The interval indicates that the posted data are not sufficiently precise to distinguish among a range of possible effects, including no difference. The p-value does not measure clinical importance or the probability that a particular interpretation is true.

The secondary outcomes provide additional, but unadjusted, comparisons. Their uncertainty, the lack of reported multiplicity methods, and the absence of a documented analysis plan mean that they should be interpreted cautiously. The safety counts are descriptive and do not constitute a comparative safety analysis.

Finally, the registry status is terminated, but the reason is not reported. The record does not provide the original sample-size justification, interim-analysis details, or missing-data methods. These limitations do not erase the posted observations, but they constrain the conclusions that can be drawn from them. The results describe this trial record; they are not medical advice and do not establish whether a treatment should be used.

17. Why This Trial Matters Statistically

This trial illustrates why the design question must be kept distinct from the broad clinical question. Because participants received golimumab before randomization, and randomization occurred among Week 16 responders, the comparison addresses continuation versus placebo withdrawal after initial response. The primary estimate cannot be read as a comparison of starting golimumab against starting placebo in the full enrolled population.

It also illustrates the difference between a point estimate and a precise conclusion. The golimumab group had a numerically higher percentage without flare, but the confidence interval includes zero and extends in both directions. Reporting the estimate together with its interval gives a more faithful account of the evidence than focusing on the arm percentages alone.

The record further shows why registry outcomes and analysis details need to be read together. A defined flare rule makes the clinical outcome operational, while missing-data methods, multiplicity handling, and the prespecified analysis plan help establish how reliably the posted comparison answers its question. Those statistical details are not reported in the registry record, so the numerical result has to be interpreted with that uncertainty in mind.

Finally, planning calculations based on an observed effect are not a substitute for prospective design assumptions. They can illustrate how smaller target effects require more participants, but they do not reveal the trial's original rationale or its planned precision. Keeping these distinctions clear is important when assessing a randomized trial without a complete statistical record.

18. Limitations

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

The registry status is terminated, but the reason is not reported in the registry record. The status alone does not explain whether termination was related to recruitment, safety, efficacy, operational considerations, or another cause. No such explanation should be inferred.

The enrolled population and primary analysis population differ by design. The primary comparison is restricted to Week 16 ACR Ped 30 responders who were randomized after receiving golimumab. Consequently, the result does not directly describe all 173 enrolled participants or people who did not respond by Week 16. The registry lists 76 participants in the placebo group and 78 in the golimumab group for the primary endpoint.

The available arm descriptions are truncated, and additional treatment and study-procedure details are not reported in the registry record. The record also does not state the reason for termination, the original sample-size justification, whether interim analyses were planned, or the full statistical analysis plan. There are no reported analyses listed.

Missing-data procedures, the treatment of incomplete flare assessments, and the method used for confidence intervals are not reported. The record also does not describe a multiplicity strategy for the primary and secondary outcomes. These gaps limit evaluation of the robustness of the comparisons and the degree to which the posted results reflect a prespecified analysis.

Safety information is presented across groups with different treatment histories. Exposure duration and a comparative safety analysis are not reported, and the denominator for the listed serious-event term percentages is not clarified. These data are therefore descriptive rather than a basis for direct treatment-safety comparisons.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of the Safety and Efficacy of CNTO 148 (Golimumab) in Children With Juvenile Idiopathic Arthritis (JIA) and Multiple Joint Involvement Who Have Poor Response to Methotrexate (GO KIDS) — NCT01230827.
• Registry record last updated 2016-04-04; status last verified 2016-03.
• Results first posted 2014-09-29.
• 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.

22. Record Summary

The registry describes a Phase 3 randomized-withdrawal study of subcutaneous golimumab in participants with active polyarticular juvenile idiopathic arthritis despite standard therapy. The trial is listed as randomized, parallel-group, and triple-masked, with enrollment of 173 and terminated status.

For the primary comparison, participants who responded to golimumab at Week 16 were randomized to continue golimumab or receive placebo. The endpoint was absence of disease flare through Week 48. The posted percentages were 59.0% with golimumab and 52.6% with placebo; the risk difference was 0.063, with a confidence interval from -0.093 to 0.22 and an unadjusted p-value of 0.428.

The estimate is uncertain, and the record does not report the reason for termination, the original design assumptions, missing-data methods, multiplicity handling, or a full analysis plan. The secondary and safety results should be interpreted in light of those limitations.