A Phase 3 Study of NI-071 in Participants With Rheumatoid Arthritis (RADIANCE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 3 Study of NI-071 in Participants With Rheumatoid Arthritis (RADIANCE) (NCT02990806), a randomized phase 3 study. The primary outcome is Stage 1: Percentage of Participants Who Achieved 20 Percent (%) American College of Rheumatology C-reactive Protein (ACR20-CRP) Response Rate at Week 22.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-blind, multicenter, Phase 3 study with a crossover model and three stages. The trial was sponsored by Nichi-Iko Pharmaceutical Co., Ltd. Enrollment was 683, and the record lists the study as completed. Its purpose was to assess similarity of NI-071, a proposed biosimilar to infliximab, to US REMICADE in participants with rheumatoid arthritis not adequately responding to methotrexate.

Stage 1 compared NI-071 with US Remicade. Both groups received 3 mg/kg by intravenous infusion at Weeks 0, 2, 6, and 14. The primary endpoint was measured at Week 22. The Stage 1 analysis population was defined as all randomized participants, irrespective of protocol deviations or premature discontinuation.

During Stage 2, participants originally assigned to Remicade were re-randomized. One group continued Remicade every 8 weeks from Week 22 through Week 54. The other received NI-071 at Week 22, Remicade at Week 30, and NI-071 at Weeks 38, 46, and 54. Participants were followed through Week 62. The NI-071 group continued NI-071 dosing through Week 54 and was also followed through Week 62.

The registry record does not report the original design’s detailed sample-size assumptions, the randomization procedures, or the masking procedures beyond describing the study as double-blind. It also does not report a fuller statistical analysis plan in the information summarized for these results. Those details should not be inferred from the staged treatment schedule.

4. Participant Flow and Accounting

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

Before assignment: The study consisted of 3 stages: the biosimilarity stage (Stage 1), the interchangeability stage (Stage 2), and the safety follow-up stage (Stage 3). A total of 683 participants were randomized in a 2:1 ratio to the Remicade-US and NI-071 groups during Stage 1. In Stage 2 participants in the original Remicade-US group were re-randomized (1:1) to a Remicade-US group and a Switch group (to assess the effects of switching between Remicade-US and NI-071).

Stage 1 (22 Weeks)

Reasons for not completing this period:

Stage 2 (32 Weeks)

Reasons for not completing this period:

Stage 3 (Safety Follow-up) (8 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intent to Treat (ITT) included all participants who were randomized, irrespective of any deviation from the protocol or premature discontinuation. Data for this outcome measure was planned to be collected and analyzed for Stage 1.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: The intent-to-treat (ITT) population included all participants who were randomized, irrespective of any deviation from the protocol or premature discontinuation.

6. Primary Endpoint

The registry lists the primary outcome as Stage 1: Percentage of Participants Who Achieved 20 Percent (%) American College of Rheumatology C-reactive Protein (ACR20-CRP) Response Rate at Week 22, measured over At Week 22.

The primary endpoint was the percentage of participants who achieved an ACR20-CRP response at Week 22 in Stage 1. ACR20 is a binary outcome: each participant is classified as either a responder or a non-responder. A response required improvement from baseline of at least 20% in both tender or painful joint count and swollen joint count, together with improvement in at least three of five additional measures. Those measures were participant and physician global assessments of disease activity, participant pain assessment, the Health Assessment Questionnaire-Disability Index, and C-reactive protein.

This composite definition combines joint findings, patient- and clinician-reported assessments, function, and an inflammatory marker. Using a responder classification gives a clinically interpretable summary of whether a participant met the stated improvement criteria, but it also compresses changes of differing size into two categories. A participant who just meets the criteria and one with larger improvements are both counted as responders.

The registry gives the endpoint as a percentage and reports a 95% confidence interval for each group. The primary comparison is therefore about the proportion meeting the response definition, not the average amount of change in each component. The record identifies the intent-to-treat population and says this outcome was planned for Stage 1. It does not report the handling of missing Week 22 measurements or the specific rules used to classify such cases.

7. Results Posted in the Registry

• Stage 1: Remicade-US Group: 53.0% (241/455) versus 56.6% (129/228) on control; risk difference -3.6 percentage points (95% CI -11.5 to 4.3), risk ratio 0.94 (0.81–1.08); unadjusted two-proportion z-test p = 0.372.

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.

Stage 2 and 3: Minimum Observed Serum Concentration (Cmin) of NI-071 and Remicade US

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Stage 2 and Stage 3: Remicade US to Remicade-US Group: mean 754.10 versus 839.10 on control; difference -85.00 (95% CI -384.06 to 214.06), standardized effect d = -0.06; z-test p = 0.577.
  • Stage 2 and Stage 3: Remicade US to Switch Group: mean 762.60 versus 839.10 on control; difference -76.50 (95% CI -360.37 to 207.37), standardized effect d = -0.06; z-test p = 0.597.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 2 and Stage 3: Remicade US to Remicade-US Group and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 2 and Stage 3: Remicade US to Switch Group and the control. The interval gives the range of effects that remain compatible with the data.

Stage 2 and 3: Time to Reach the Maximum Serum Concentration (Tmax) of NI-071 and Remicade US

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Stage 2 and Stage 3: Remicade US to Remicade-US Group: mean 41.57 versus 52.37 on control; difference -10.80 (95% CI -61.83 to 40.23), standardized effect d = -0.05; z-test p = 0.678.
  • Stage 2 and Stage 3: Remicade US to Switch Group: mean 32.98 versus 52.37 on control; difference -19.39 (95% CI -68.32 to 29.54), standardized effect d = -0.09; z-test p = 0.437.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 2 and Stage 3: Remicade US to Remicade-US Group and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 2 and Stage 3: Remicade US to Switch Group and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With TEAEs of Special Interest

• 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:
  • Stage 1: Remicade-US Group: 15.1% (68/451) versus 14.5% (33/227) on control; risk difference 0.5 percentage points (95% CI -5.1 to 6.2), risk ratio 1.04 (0.71–1.52); unadjusted two-proportion z-test p = 0.852.
  • Stage 2 and Stage 3: Remicade US to Remicade-US Group: 16.9% (43/254) versus 14.5% (33/227) on control; risk difference 2.4 percentage points (95% CI -4.1 to 8.9), risk ratio 1.16 (0.77–1.77); unadjusted two-proportion z-test p = 0.473.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 1: Remicade-US Group and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 2 and Stage 3: Remicade US to Remicade-US Group and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary outcomes, including DAS28-CRP and DAS28-ESR changes, ACR20 response outcomes, pharmacokinetic measures, and safety measures across stages and visits. The available secondary-result entries include serum concentration, time to maximum concentration, and treatment-emergent adverse events. The record also lists 32 posted secondary results overall, but the outcome descriptions alone do not establish a consistent direction of effect across every measure.

These secondary outcomes address related but distinct questions. Disease activity scores and response rates describe clinical measures over follow-up, while serum concentration and time-to-maximum-concentration outcomes describe pharmacokinetic characteristics. Safety outcomes describe events rather than efficacy. They can provide context for the primary Week 22 response comparison, but they are not interchangeable measures and should not be combined into a single claim about similarity.

The primary result concerns a defined Stage 1 response endpoint at a particular visit. Later outcomes include different visits, stages, treatment sequences, and measurement types. Their results may help characterize the broader study, but they do not automatically confirm or overturn the primary comparison. The registry record does not report enough of the full statistical plan to establish which secondary outcomes were confirmatory.

As a general statistical issue, examining many outcomes and time points creates multiple opportunities for apparently notable findings. Unless the analysis plan controls this multiplicity, unadjusted secondary results carry less weight as confirmatory evidence. The multiplicity strategy is not reported in the registry record. Secondary patterns should therefore be read as context and not as a collection of independent confirmations.

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

• Stage 1: Change From Baseline in the Disease Activity Score Based on 28 Joints (DAS28) C-reactive Protein (CRP) at Weeks 2, 6, 14, 18, and 22
• Stage 2 and 3: Change From Baseline in the Disease Activity Score Based on 28 Joints (DAS28) C-reactive Protein (CRP) at Weeks 26, 30, 34, 38, 42, 46, 50, 54, 58, and 62
• Stage 1: Change From Baseline in the Disease Activity Score Based on 28 Joints (DAS28)-Erythrocyte Sedimentation Rate (ESR) at Weeks 2, 6, 14, 18, and 22
• Stage 2 and 3: Change From Baseline in the Disease Activity Score Based on 28 Joints (DAS28)-Erythrocyte Sedimentation Rate (ESR) at Weeks 26, 30, 34, 38, 42, 46, 50, 54, 58, and 62
• Stage 1: Percentage of Participants Who Achieved 20 Percent (%) American College of Rheumatology C-reactive Protein (ACR-CRP) Response Rate
• Stage 2 and 3: Percentage of Participants Who Achieved 20 Percent (%) American College of Rheumatology C-reactive Protein (ACR-CRP) Response Rate
• Stage 1: Percentage of Participants Who Achieved Greater Than or Equal to (>=) 20% American College of Rheumatology (ACR20) Response Using Erythrocyte Sedimentation Rate (ESR)
• Stage 2 and 3: Percentage of Participants Who Achieved Greater Than or Equal to (>=) 20% American College of Rheumatology (ACR20) Response Using Erythrocyte Sedimentation Rate (ESR)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary, because each participant either met the ACR20-CRP response criteria or did not. For a binary endpoint, the group response percentage estimates the proportion classified as responders. The primary comparison can be expressed as a difference between these proportions. A confidence interval around that difference describes a range of values compatible with the data and the analysis assumptions; it is not a range containing a guaranteed proportion of future trial results.

What the confidence interval tells readers

The sponsor reported a percentage difference of 3.6, with a 95% confidence interval from -4.3 to 11.5. The interval spans zero, so the posted analysis does not precisely distinguish a difference in one direction from no difference or a difference in the other direction. A 95% confidence interval is a measure of statistical uncertainty under the method used. It does not mean that there is a 95% probability that the fixed true effect lies inside this particular interval.

The group-specific intervals describe uncertainty in each group’s response percentage, while the interval for the difference addresses uncertainty in the contrast. The latter is more directly relevant to the primary comparative question. Comparing the endpoints of the two group-specific intervals is not a substitute for the reported interval for the between-group difference.

How to read the unadjusted recalculation

The recalculated comparison uses the posted response counts and denominators to form a simple, unadjusted contrast. Its p-value is 0.372. A p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be if that null and the calculation assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect.

This recalculation is not necessarily the same as the sponsor’s primary analysis. The registry labels the sponsor’s result as an equivalence analysis, while the recalculation is an unadjusted comparison from summary counts. A formal equivalence analysis ordinarily depends on a prespecified margin and its corresponding decision procedure. The equivalence margin and detailed analysis method are not reported in the registry record. Consequently, the recalculated p-value should be read as a descriptive supplemental calculation, not as the trial’s primary test.

Why the analysis population matters

The primary outcome description defines the intent-to-treat population as all randomized participants, regardless of protocol deviations or premature discontinuation. This definition preserves the randomized assignment as the basis for analysis. The registry record does not specify how missing endpoint values were handled, whether all randomized participants contributed a Week 22 response classification, or whether other analysis populations were used for the sponsor’s result. These omissions matter because missing outcome data and analysis-population choices can affect estimated response proportions.

Randomization is intended to make treatment groups comparable with respect to measured and unmeasured characteristics on average. Double masking can limit some influences on care and outcome assessment. The record states that the trial was randomized and double-blind but does not provide enough detail to describe allocation concealment, masking roles, or the exact randomization implementation.

Multiplicity and secondary outcomes

The registry lists many secondary outcomes, including disease activity measures and response rates at multiple visits, as well as pharmacokinetic measures and safety outcomes. Testing or estimating many outcomes can increase the chance of finding an apparently notable result by chance. The record does not report whether multiplicity adjustments, a hierarchical testing plan, or other control of multiple comparisons was used. Secondary results should therefore be treated as supportive or exploratory unless a prespecified analysis plan establishes otherwise.

These methods explanations are general statistical context. The exact analysis methods for the sponsor’s primary result, missing-data rules, equivalence margin, and multiplicity strategy are not reported in the registry record. No method should be assumed to have been used solely because it is common in clinical trials.

11. Confidence Intervals and Precision

The central precision result is the sponsor-reported percentage difference of 3.6, with a 95% confidence interval from -4.3 to 11.5. The lower and upper limits lie on opposite sides of zero. Thus, the reported data do not rule out no difference, and the interval allows a range of effects in either direction. The estimate is informative about the approximate contrast, but its uncertainty limits how narrowly the difference can be described.

The group-level response estimates also have uncertainty: NI-071 was 56.6% with a 95% confidence interval from 50.1% to 63.0%, while Remicade was 53.0% with a 95% confidence interval from 48.4% to 57.6%. These separate intervals give context for the estimated proportions. The confidence interval for the direct difference is the more appropriate interval for judging precision in the comparison itself.

In general, an interval becomes narrower when an estimate is more precise and wider when uncertainty is greater. Its width reflects factors such as the amount of information and the variability in the data, as well as the statistical method. The registry record does not provide enough information to evaluate all assumptions behind the sponsor’s interval or to establish how missing values were treated.

Precision and equivalence are related but not interchangeable. To interpret an equivalence result, readers need the prespecified margin as well as the confidence interval and analysis method. The equivalence margin is not reported in the registry record, so the interval’s position cannot be assessed against that decision boundary. Nor does a confidence interval that includes zero alone establish similarity.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the original trial’s design calculations. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The illustrative effect to detect is set at the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

For these comparisons, the entries refer to participants per arm, not a total across arms. The 80% power column describes the planned number of participants per arm under the stated assumptions to give an 80% chance of detecting the specified effect if that effect were true. The 90% power column uses the same general interpretation but targets a 90% chance. These are design-planning quantities, not guarantees about what a future study will find.

The rows that plan for 100%, 75%, and 50% of the observed effect illustrate how the assumed effect size changes the planning requirement. Smaller effects are harder to distinguish from random variation and therefore require more participants under the same assumptions. These figures are not observed power and should not be interpreted as a retrospective measure of whether the completed trial was adequate.

The illustrations are tied to the effect estimate from this trial, which itself is uncertain. They do not establish a recommended sample size, account for every feature of a possible future protocol, or reproduce the sponsor’s design process. The registry record does not report the original design assumptions, and the illustrative calculation should be kept separate from the sponsor’s primary equivalence analysis.

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 = 0.566; treatment proportion p₁ = 0.530; average p̄ = 0.548.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7039 = 1.3796.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7034 = 0.5920.
4. n = (1.3796 + 0.5920)² / (-0.0361)² = 2,979.6, rounded up to 2,980 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 <- 0.565789473684211                          # control proportion
p1 <- 0.52967032967033                          # 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(2990806)
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 = 2,980 (80% power), 3,989 (90% power)
 75% of observed effect: n per arm = 5,289 (80% power), 7,080 (90% power)
 50% of observed effect: n per arm = 11,877 (80% power), 15,899 (90% power)
power.prop.test: 2979.6 
Simulated power at n = 2,980 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary result as an equivalence analysis: a percentage difference of 3.6 with a 95% confidence interval from -4.3 to 11.5. No sponsor p-value is listed. The registry record does not report the equivalence margin or enough methodological detail to independently reproduce the sponsor’s analysis or verify the decision rule.

The simple recalculation from posted response counts is unadjusted and gives an unadjusted p-value of 0.372. It is a check based on the summary counts, not a substitute for the sponsor’s analysis. The sponsor’s own analysis takes precedence over a simple recalculation when the two differ, because it is the reported trial analysis and may reflect prespecified methods not captured by a summary-count calculation.

In this case, the recalculation does not indicate a materially different overall interpretation from the sponsor’s reported estimate: both are compatible with uncertainty about the direction of the contrast. Neither the recalculation nor the reported confidence interval alone supplies the missing equivalence margin. The sponsor’s label of equivalence analysis should be reported as such, without converting it into a claim that the criterion was met when the required margin and decision details are not in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome description defines the intent-to-treat population as all randomized participants, regardless of protocol deviation or premature discontinuation. This is an important population definition because it ties the analysis to randomized assignment. However, the registry record does not specify whether every randomized participant had an evaluable Week 22 outcome or how missing values were classified or imputed. It also does not report sensitivity analyses addressing missing outcome data.

The record lists numerous secondary measures and repeated assessment times across the three stages. In general, testing many outcomes or time points increases the chance that some results will appear notable by chance, even when there is no underlying effect. A prespecified hierarchy, adjustment, or other multiplicity strategy can address this issue. The registry record does not report whether such a strategy was used, so the secondary findings should not be assumed to have controlled family-wise error or another multiplicity criterion.

The sponsor’s primary analysis is labelled equivalence, but the equivalence margin and detailed decision procedure are not reported in the registry record. Those details are necessary to assess what range of differences the study was designed to regard as sufficiently similar and how the conclusion was reached. The record also does not report the full model specification or all analysis assumptions for the sponsor’s result.

Other details that are not reported in the registry record include interim analyses, stopping rules, and the original sample-size justification. Their absence from the record does not establish that these procedures were or were not used. It means they cannot be incorporated into an interpretation of the posted results. The safest reading separates the information that is stated—the endpoint definition, analysis population description, and sponsor-reported estimate—from design and analysis details that remain unreported.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anaphylactic reaction (1.2%), chronic sinusitis (0.5%), extradural abscess (0.5%), gastroenteritis (0.5%), influenza (0.5%).

For serious adverse events, the registry lists 19 affected participants among 227 at risk in the NI-071 group, 41 among 451 in the Stage 1 Remicade-US group, 28 among 254 in the Remicade-to-Remicade group, and 13 among 197 in the Remicade-to-switch group. The record lists one death in the NI-071 group and one in the Stage 1 Remicade-US group; it lists no deaths in either Stage 2 and Stage 3 Remicade sequence group.

The groups cover different treatment stages and sequences, and their at-risk denominators are not identical. The Stage 2 groups also arise from participants who received Remicade in Stage 1 and were re-randomized. These figures should therefore be read in their stated group and follow-up context, not combined into a single comparison or treated as if all groups were concurrent randomized arms for the same period.

The registry lists anaphylactic reaction at 1.2% among the most frequent serious-event terms, followed by chronic sinusitis, extradural abscess, gastroenteritis, influenza, and kidney infection at 0.5% each. These listed terms do not describe every event or establish a causal relationship. The posted counts are descriptive safety information and are not, by themselves, a formal comparative safety analysis.

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

The primary result describes the proportion meeting the registry’s ACR20-CRP response definition at Week 22 in the two Stage 1 treatment groups. The posted percentages were 56.6% for NI-071 and 53.0% for US Remicade. The sponsor reported a percentage difference of 3.6 with a 95% confidence interval from -4.3 to 11.5. This is a summary of the observed endpoint and the uncertainty around the comparison, not a guarantee about an individual participant’s outcome.

The interval includes zero and spans values on either side of zero. The estimate therefore does not precisely establish the direction of a difference. The registry labels the sponsor analysis as equivalence, but the equivalence margin and complete decision method are not reported in the registry record. The response percentages and confidence interval should not be turned into a definitive equivalence claim without those details.

The result applies to the specific Stage 1 population, treatment schedule, follow-up point, and composite response definition recorded in the trial. It does not by itself answer whether the products have identical effects, whether every component of the composite changed similarly, or whether results would be the same in other populations or settings. It also does not resolve questions about longer-term outcomes or all safety outcomes.

Later-stage findings concern continued treatment or switching sequences, with follow-up through Week 62. Those data address different questions from the Stage 1 primary endpoint and should be interpreted in their own design context. Similarly, secondary efficacy, pharmacokinetic, and safety measures provide additional information but cannot substitute for the primary comparison or establish a broader conclusion on their own.

Overall, the posted data support a cautious description: the Stage 1 response proportions were in the ranges reported, and the estimated between-group difference has meaningful uncertainty. Statistical uncertainty should be kept distinct from clinical importance and from the sponsor’s stated similarity objective. The registry record does not supply all information needed to assess the sponsor’s equivalence decision independently.

18. Why This Trial Matters Statistically

This trial is statistically notable because its stated objective was similarity, while the primary outcome was a binary response proportion at a specific visit. Similarity and equivalence questions are not answered simply by observing that two group percentages are close or that a conventional test does not identify a difference. A formal interpretation depends on a prespecified acceptable margin, an appropriate analysis, and adequate precision. The registry labels the sponsor’s analysis as equivalence, but the margin is not reported in the registry record.

The study also has a staged treatment structure. Stage 1 provides the direct randomized comparison used for the primary endpoint. Later treatment sequences include continued Remicade and switching between Remicade and NI-071. This distinction matters statistically: later observations are shaped by prior treatment and re-randomization, so they should not be casually combined with the initial comparison.

The posted confidence interval gives readers more information than a point estimate alone. It shows that uncertainty remains about the size and direction of the primary contrast. The simple unadjusted recalculation provides a transparent check from the posted counts, while the sponsor’s own analysis remains the primary reported result.

Finally, the trial illustrates why analysis populations, missing-data handling, multiplicity, and prespecified methods matter. The record states an intent-to-treat definition and a broad set of secondary outcomes, but several key analysis details are not reported. Explicitly recognizing those limits helps distinguish the observed data from conclusions that require additional design and analysis information.

19. Limitations

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

The registry record does not report the equivalence margin, the detailed method used for the sponsor’s primary analysis, or the full prespecified statistical analysis plan. This limits independent assessment of the sponsor’s equivalence interpretation. The original sample-size justification and design assumptions are also not reported in the registry record; the available sample-size illustrations are not the trial’s original design calculations.

Missing-data procedures for the Week 22 primary endpoint are not reported in the registry record. Although the outcome description defines an intent-to-treat population, it does not specify how participants without an observed Week 22 response assessment were handled or whether sensitivity analyses were conducted. The record also does not report whether interim analyses or stopping rules were used.

The Stage 2 and Stage 3 results arise from a multistage schedule, including re-randomization of participants who received Remicade during Stage 1 and a switching sequence. Those results answer questions different from the initial Stage 1 comparison. The safety groups span different stages and follow-up contexts, so their counts should not be treated as a single concurrent comparison.

The registry lists many secondary outcomes and repeated time points, but the multiplicity strategy is not reported in the registry record. The posted secondary results should therefore be interpreted cautiously as a set of distinct measures, not as independent confirmatory tests. The record also does not provide all operational details of randomization or masking beyond describing the trial as randomized and double-blind.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase 3 Study of NI-071 in Participants With Rheumatoid Arthritis (RADIANCE) — NCT02990806.
• Registry record last updated 2023-01-30; status last verified 2023-01.
• Results first posted 2023-01-25.
• 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

NCT02990806 is a completed randomized, double-blind, multicenter Phase 3 study of NI-071 and US-licensed Remicade in participants with rheumatoid arthritis not adequately responding to methotrexate. The trial used three stages, including a Stage 1 active-comparator assessment and later continued-treatment or switching sequences.

The primary endpoint was the Stage 1 percentage achieving ACR20-CRP response at Week 22. Posted response percentages were 56.6% for NI-071 and 53.0% for Remicade. The sponsor reported an equivalence analysis with a percentage difference of 3.6 and a 95% confidence interval from -4.3 to 11.5. The equivalence margin and several analysis details are not reported in the registry record, so the estimate is best read alongside that limitation.

The record includes secondary clinical, pharmacokinetic, and safety outcomes. Their interpretation depends on their distinct measures, stages, and time points, and the multiplicity strategy is not reported in the registry record.