Dose Finding Study of Namilumab in Combination With Methotrexate in Participants With Moderate to Severe Rheumatoid Arthritis (RA): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose Finding Study of Namilumab in Combination With Methotrexate in Participants With Moderate to Severe Rheumatoid Arthritis (RA) (NCT02379091), a randomized phase 2 study. The primary outcome is Change From Baseline in Disease Activity Score 28 C-Reactive Protein (DAS28-CRP) at Week 12.

2. Clinical Question

The study was designed to establish proof of concept and identify an efficacious dose in the stated rheumatoid arthritis populations. Its primary outcome was continuous, so the registry reports least-squares mean changes and between-group contrasts rather than only the proportion of participants meeting a response threshold. The results describe this trial’s groups and analysis; they do not, by themselves, establish how the findings apply to people outside the study population.

3. Trial Design

This was a randomized, double-blind, placebo-controlled, parallel-group phase 2 study. The registry reports quadruple masking. Enrollment was 108, and the study status is completed. The official title describes a 24-week study evaluating three namilumab doses with methotrexate. The primary outcome was change from Baseline in DAS28-CRP at Week 12.

The four primary-outcome groups were placebo and namilumab 20 mg/mL, 80 mg/mL, and 150 mg/mL. Methotrexate was part of the study context for the treatment comparisons. The arm descriptions state that participants were assessed for response using improvement in both swollen and tender joint counts, and that treatment continuation depended on response. The descriptions are truncated, so the complete response-based treatment procedure is not reported in the registry record.

For the primary analysis, the stated population was the Full Analysis Set: participants in the safety analysis set with at least one valid post-baseline DAS28-CRP assessment in the double-blind period up to Week 12, and data available at Baseline and Week 12 for analysis. The primary-outcome group counts were 24 for placebo, 25 for namilumab 20 mg/mL, 22 for namilumab 80 mg/mL, and 26 for namilumab 150 mg/mL. These analysis counts do not need to equal total enrollment, because the endpoint analysis used its defined population and available measurements.

Randomization procedures, allocation ratios, concealment details, site counts, and the original sample-size justification are not reported in the registry record. The record also does not explain how the response-based treatment procedure interacted with continued masking or later assessments. Those details should not be inferred from the short arm descriptions.

4. Participant Flow and Accounting

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

Before assignment: Participants with a diagnosis of moderate to severe Rheumatoid Arthritis were enrolled equally in one of 4 treatment groups: placebo or 20, 80, 150 mg/mL namilumab.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants from the Full Analysis Set (FAS), all participants in the safety analysis set who had at least 1 valid post-baseline assessment of DAS28-CRP in double-blind period up to Week 12, with data available at Baseline and Week 12 for analysis.

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: Safety analysis set includes all participants who received at least 1 dose of double-blind study drug.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Disease Activity Score 28 C-Reactive Protein (DAS28-CRP) at Week 12, measured over Baseline and Week 12.

The primary endpoint was change from Baseline in Disease Activity Score 28 C-Reactive Protein (DAS28-CRP) at Week 12. It is a continuous score based on the tender joint count across 28 joints, swollen joint count across 28 joints, the participant’s global assessment of disease activity on a visual analog scale, and C-reactive protein. The possible score ranges from 0 (best) to approximately 10 (worst). The registry states that scores below 2.6 indicate best disease control and scores above 5.1 indicate worse disease control. A negative change from Baseline indicates improvement.

Using a composite continuous measure allows the analysis to reflect several components of disease activity in one outcome. In general, continuous outcomes retain information about the magnitude of change rather than reducing results to whether a participant did or did not cross a response cutoff. That can make average change useful for comparing groups, while still leaving open whether any particular participant experienced a similar change.

The registry reports least-squares mean changes with standard errors and describes a mixed model repeated measures analysis. The primary question is the between-group difference in mean change, not simply whether each group’s score moved from Baseline. Interpreting the contrast also requires attention to its uncertainty, analysis population, and the fact that the registry does not report a clinically important between-group difference for this endpoint.

7. Results Posted in the Registry

• Namilumab 20 mg/mL: mean -1.38 versus -0.77 on control; difference -0.61 (95% CI -1.42 to 0.20), standardized effect d = -0.42; z-test p = 0.138.
• Namilumab 80 mg/mL: mean -1.36 versus -0.77 on control; difference -0.59 (95% CI -1.42 to 0.24), standardized effect d = -0.41; z-test p = 0.162.
• Namilumab 150 mg/mL: mean -1.69 versus -0.77 on control; difference -0.92 (95% CI -1.72 to -0.12), standardized effect d = -0.63; z-test p = 0.025.

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.

ACR Numeric (N) Index (ACRn) at Week 12

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Namilumab 20 mg/mL: mean 3.97 versus -17.25 on control; difference 21.22 (95% CI -24.29 to 66.73), standardized effect d = 0.26; z-test p = 0.361.
  • Namilumab 80 mg/mL: mean 19.68 versus -17.25 on control; difference 36.93 (95% CI -9.29 to 83.15), standardized effect d = 0.46; z-test p = 0.117.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Namilumab 20 mg/mL 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 Namilumab 80 mg/mL and the control. The interval gives the range of effects that remain compatible with the data.

ACR Numeric (N) Index (ACRn) at Week 24

• 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:
  • Namilumab 20 mg/mL: mean 35.35 versus 34.04 on control; difference 1.31 (95% CI -22.88 to 25.50), standardized effect d = 0.03; z-test p = 0.915.
  • Namilumab 80 mg/mL: mean 44.66 versus 34.04 on control; difference 10.62 (95% CI -11.13 to 32.37), standardized effect d = 0.27; z-test p = 0.339.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Namilumab 20 mg/mL 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 Namilumab 80 mg/mL and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in DAS28-CRP at Week 24

• 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:
  • Namilumab 20 mg/mL: mean -2.37 versus -1.75 on control; difference -0.62 (95% CI -1.56 to 0.32), standardized effect d = -0.51; z-test p = 0.195.
  • Namilumab 80 mg/mL: mean -2.20 versus -1.75 on control; difference -0.45 (95% CI -1.44 to 0.54), standardized effect d = -0.35; z-test p = 0.374.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Namilumab 20 mg/mL 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 Namilumab 80 mg/mL and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes listed in the registry span response thresholds, continuous disease activity measures, and pain. The posted secondary results include ACR Numeric Index at Week 12 and Week 24 and change in DAS28-CRP at Week 24. The registry lists other secondary outcomes, including ACR20, ACR50, ACR70, earlier DAS28-CRP changes, and pain reduction, but results for all listed outcomes are not present in the record; those results are not reported in the registry record.

Across the posted continuous secondary outcomes, estimated group patterns vary by endpoint and visit. This broad pattern should be read as supplementary context rather than as a substitute for the Week 12 primary analysis. The Week 24 measures use different reported summaries in some cases, and the registry does not provide a complete set of sponsor analyses for these outcomes. The Week 12 primary endpoint remains the specified main comparison; secondary measures can add context but do not independently settle the primary question.

In general, testing many outcomes and dose comparisons increases the chance that some apparently notable findings arise by chance. Unadjusted secondary results carry less weight when the registry does not report a multiplicity procedure, a hierarchy for testing, or a clear distinction between confirmatory and exploratory outcomes. The record’s count of outcome measures does not itself establish how the sponsor controlled multiplicity. A result on one secondary endpoint should therefore be interpreted with its estimate and uncertainty, the number of analyses considered, and the lack of reported adjustment in mind.

The registry does not report enough information to reconcile all outcome definitions and analysis populations across visits. Secondary results are best treated as descriptive evidence that may motivate further evaluation, rather than as standalone confirmation of a treatment effect or a dose pattern.

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

• Percentage of Participants Achieving American College of Rheumatology 20% (ACR20), 50% (ACR 50) and 70% (ACR70) Response at Weeks 12 and 24
• ACR Numeric (N) Index (ACRn) at Week 12
• ACR Numeric (N) Index (ACRn) at Week 24
• Change From Baseline in DAS28-CRP at Weeks 2, 6, and 10
• Change From Baseline in DAS28-CRP at Week 24
• Percentage of Participants With a Reduction of Pain as Measured Using a Visual Analog Scale (VAS) at Weeks 2, 12 and 24

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, and the sponsor reports least-squares means and between-group contrasts. A least-squares mean is a model-based group estimate: it reflects the fitted analysis rather than necessarily being the simple arithmetic average of the observed values. That distinction matters because the primary analysis used a model incorporating treatment, visit, study site, previously failed medication, and specified interactions, with baseline value as a covariate. The registry describes participant as a random effect and an unstructured covariance structure.

Why use repeated measurements?

In general, a mixed model repeated measures analysis can use observations collected at multiple visits and account for the fact that repeated observations from one participant are related. The primary outcome description states that the model included main effects for study site, treatment, visit, and previously failed medication; interactions between visit and treatment and between visit and previously failed medication; and an interaction between visit and baseline value as a covariate. Participant was included as a random effect. The model’s unstructured covariance structure allows the relationships among repeated measurements to be estimated without imposing a simple pattern. These are general interpretations of the named modeling features; the registry does not report additional diagnostic checks or sensitivity analyses.

What does the contrast estimate?

The treatment contrast compares the fitted average change in a namilumab group with the fitted average change in placebo. A negative contrast in this analysis corresponds to a more negative change in the namilumab group, given the registry’s definition that negative change indicates improvement. The contrast is not the same as a within-group change, and it does not mean that every participant had that difference. Its uncertainty is reflected by the confidence interval and by the statistical test reported by the sponsor.

Why distinguish sponsor results from recalculations?

The recalculated comparisons are simple, unadjusted calculations from the posted group summaries. They do not reproduce the sponsor’s model, its covariate adjustments, or its handling of repeated observations. The group standard errors also require an approximation to derive standard deviations for these recalculations. In general, a simple summary-statistic calculation and an adjusted repeated-measures analysis can differ because they use different information and assumptions. The registry record flags a discrepancy; the sponsor’s own analysis therefore takes precedence. The recalculations are descriptive checks, not replacements for the prespecified or sponsor analysis.

What do p-values and confidence intervals contribute?

In general, a p-value measures how unusual the data, or more extreme data, would be under a specified null model. It does not measure the probability that the null hypothesis is true, and it does not describe the size or practical importance of a contrast. A confidence interval gives a range of estimates compatible with the data and analysis at its stated confidence level. A wide interval signals imprecision; an interval spanning zero includes both directions of contrast under the model. Neither measure resolves the possibility of bias, model misspecification, or multiplicity.

The sponsor reports ANOVA for the primary comparisons, while the endpoint description specifies the mixed model repeated measures model. The registry does not explain the relationship between those labels or provide a fuller statistical analysis plan. The original sample-size justification, interim analyses, model diagnostics, and sensitivity analyses are not reported in the registry record. No unreported choices should be assumed.

11. Confidence Intervals and Precision

The sponsor’s 95% confidence intervals express the uncertainty around the primary between-group estimates under the reported analysis. For namilumab 20 mg/mL, the estimate is -0.61 and the interval runs from -1.31 to 0.09. For 80 mg/mL, the registry reports an LS Mean value of -0.60 and an interval from -1.32 to 0.13. For 150 mg/mL, the LS Mean Difference is -0.92 and the interval runs from -1.61 to -0.23. The first two intervals include zero; the 150 mg/mL interval does not.

In general, a confidence interval communicates a range of values reasonably compatible with the observed data and the analysis assumptions. It is not a guarantee that the true effect lies in the interval, and it does not capture every source of uncertainty, such as unreported design choices or possible bias. An interval that includes zero is consistent with a range of contrasts on either side of no difference; it should not be read as proof that the groups are identical. An interval excluding zero still does not, by itself, establish clinical importance.

The primary analysis group counts were 24, 25, 22, and 26 across placebo and the three dose groups. The group estimates and their intervals are therefore based on relatively limited numbers of endpoint observations. The registry does not report a clinically important difference threshold, so the range of values should be considered in relation to statistical uncertainty without labeling the magnitude clinically meaningful or unimportant.

The recalculated intervals are based on simple unadjusted summaries, not the sponsor’s repeated-measures analysis. Because a discrepancy is flagged, the sponsor’s reported intervals are the appropriate primary results to prioritize. Differences between methods are part of the uncertainty in interpreting the posted record and should not be concealed by presenting recalculations as equivalent analyses.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the continuous-outcome comparisons; they are not total event counts. They are illustrative calculations based on the observed effect, not the trial’s own design. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s sample-size justification is not reported in the registry record.

The 80% power column gives the number of participants per arm calculated to provide an 80% chance of detecting the specified effect under those assumptions if that effect and model assumptions hold. The 90% power column uses a higher chance of detection and therefore generally requires more participants per arm. These figures are conditional planning illustrations, not guarantees about a future study’s result. This is not observed power.

Rows planning for 100%, 75%, and 50% of the observed effect show how the calculation changes when the target effect is smaller. A smaller effect is harder to distinguish from random variation, so more participants are needed for the same target power under otherwise unchanged assumptions. The observed effect can be an unstable basis for planning, particularly when it comes from a small study; the illustrations do not account for every design feature that may affect a real trial.

Read the planning figures in connection with the specific comparison and endpoint: the calculations use that comparison’s observed estimate and variability. They are not a reconstruction of the study’s original enrollment decision and do not establish that the trial was adequately or inadequately powered. The registry does not report the original design assumptions needed to make that judgment.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.610; pooled standard deviation σ = 1.440.
2. n = 2 × (1.96 + 0.842)² × 1.440² / -0.610² = 87.5, rounded up to 88 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
delta <- -0.61                      # observed difference in means
sigma <- 1.44014680102781                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2379091)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 88 (80% power), 118 (90% power)
 75% of observed effect: n per arm = 156 (80% power), 209 (90% power)
 50% of observed effect: n per arm = 350 (80% power), 469 (90% power)
power.t.test: 88.5 
Simulated power at n = 88 per arm: 0.797 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor reported primary analyses using ANOVA and presented least-squares results with 95% confidence intervals and p-values. These are the main primary-outcome results to use when describing the trial. The registry also permits simple unadjusted recalculations from the posted group summaries, but those calculations do not reproduce the sponsor’s model-based repeated-measures analysis.

The estimates are close in some comparisons, but the recalculated p-values differ from the sponsor’s reported p-values. For 20 mg/mL, the recalculated p-value is 0.138 and the sponsor’s is 0.086; for 80 mg/mL, the recalculated p-value is 0.162 and the sponsor’s is 0.107; for 150 mg/mL, the recalculated p-value is 0.025 and the sponsor’s is 0.010. The sponsor’s reported 80 mg/mL result is labeled LS Mean rather than LS Mean Difference, whereas the recalculated comparison is an unadjusted mean difference.

These contrasts should not be interpreted as competing versions of an identical analysis. The recalculations use posted summary statistics, while the sponsor’s reported analysis is model-based. The registry flags a discrepancy, so the sponsor’s own analysis takes precedence. The record does not provide enough detail to determine every reason for the differences or to independently reproduce the sponsor model.

15. Multiplicity, Missing Data and Analysis Populations

There are multiple dose comparisons for the primary endpoint, as well as several secondary outcomes and time points. The registry reports three sponsor primary comparisons and lists a range of secondary measures, but it does not report whether the p-values were adjusted for multiple testing, whether a testing hierarchy was used, or which secondary outcomes were designated confirmatory. The original statistical analysis plan is not reported in the registry record. Without that information, the nominal p-values should not be interpreted as if family-wise error control had been documented.

Multiplicity matters in general because the more hypotheses examined, the greater the opportunity for at least one apparently unusual result to occur by chance. This does not invalidate the reported estimates, but it affects how strongly isolated p-values support confirmatory conclusions. The posted estimates and confidence intervals remain useful descriptions of the analyses; their evidential weight depends on the full testing plan, which is not available in the registry record.

The primary population definition requires a valid post-baseline DAS28-CRP assessment during the double-blind period up to Week 12 and data at Baseline and Week 12 for analysis. The model description identifies the analysis set, but the registry does not explain in detail how missing endpoint measurements were handled, whether any imputation was used, or what assumptions about missingness were made. It also does not report sensitivity analyses to assess the influence of missing data.

Analysis populations and available observations differ across posted outcomes. For example, endpoint-specific group counts vary across the primary and secondary summaries. Such variation can reflect outcome-specific availability or analysis definitions, but the registry record does not give a complete account of the reasons. It is therefore important not to assume that every endpoint used the same participants or the same missing-data procedure.

The record also does not report interim analyses, stopping rules, or the original sample-size justification. These omissions limit assessment of how the reported comparisons fit into the trial’s full planned statistical framework. They do not change the numerical results but should temper claims about confirmatory evidence.

16. 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: asthma (4.2%), mallory-weiss syndrome (4.2%), angina pectoris (4.2%), ankle fracture (4.2%), breast cancer (4.0%).

The registry reports serious adverse events by group, with counts at risk and counts affected. During the listed groups, serious adverse events affected 0 of 27 participants in placebo, 0 of 28 in namilumab 20 mg/mL, 1 of 25 in namilumab 80 mg/mL, and 1 of 28 in namilumab 150 mg/mL. It also lists a placebo-to-namilumab 150 mg/mL group with 0 of 12 affected, and a namilumab-to-namilumab 150 mg/mL group with 4 of 24 affected. These groups should be read as separately reported categories, not combined without information on overlap and follow-up.

The registry lists serious-event terms with percentages, including asthma, Mallory-Weiss syndrome, angina pectoris, ankle fracture, breast cancer, and myocardial infarction. The record does not give enough context to attribute these listed terms to particular treatment groups or to infer causation. Death counts are not reported in the registry record.

In general, adverse-event counts describe what was recorded among participants at risk during the stated observation categories; they do not establish that treatment caused an event. The registry does not provide exposure-adjusted rates or sufficient follow-up detail for a broader comparative safety assessment. These figures should be considered alongside the trial’s size and duration, without treating them as a complete characterization of safety.

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

The primary results describe average Week 12 changes in DAS28-CRP in this randomized phase 2 study. The sponsor reported a difference with a 95% confidence interval excluding zero for the 150 mg/mL comparison, while the intervals for the 20 mg/mL and 80 mg/mL comparisons included zero. These are findings from the posted analyses, not medical advice and not a basis for an individual treatment decision.

A statistically distinguishable group estimate does not automatically show that the difference is important to participants. The registry does not report a threshold for a clinically important difference in DAS28-CRP, and the confidence intervals describe uncertainty under the analysis rather than all possible sources of uncertainty. Conversely, an interval including zero does not demonstrate equivalence or prove there is no difference. The trial was a dose-finding phase 2 study, and the record does not establish a formal dose-response pattern.

The result also does not describe each participant’s experience. Group means can conceal variation in response, and the primary outcome is a composite score rather than a direct account of every symptom or functional outcome. Secondary measures may provide additional context, but the registry does not report results for every listed secondary outcome or a multiplicity plan that would support treating isolated secondary findings as confirmatory.

The findings apply most directly to the study population and analysis definitions in the registry: participants with moderate to severe rheumatoid arthritis in the stated methotrexate-inadequate-response and TNF-inhibitor-inadequate-response groups. The record does not provide detailed demographic or clinical subgroup results to establish how effects varied within that population. Nor can a single study of this size and phase settle questions about other populations, longer-term outcomes, or treatment choices.

In short, the record offers comparative estimates and uncertainty for a defined endpoint and time point. It does not establish a universal effect, a complete safety profile, or a clinical recommendation.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares three doses against a shared placebo group using a continuous disease-activity outcome. Dose-finding studies can help estimate whether outcome patterns vary across doses and which comparisons may merit further evaluation. Here, each dose is compared with placebo, but the registry does not report a formal trend analysis, so the estimates alone should not be treated as evidence of a dose-response relationship.

The primary analysis also illustrates why the analysis method matters. The registry describes a mixed model repeated measures approach, while the sponsor’s reported comparisons are labeled ANOVA. Simple recalculations from group summaries yield different p-values, and the registry flags a discrepancy. Giving priority to the sponsor’s analysis avoids presenting a simplified recalculation as though it were the trial’s own model-based result. At the same time, the incomplete statistical documentation limits independent assessment of the analysis.

The confidence intervals emphasize that estimates can be uncertain even when group means move in a direction consistent with improvement. Considering interval width, the analysis population, and missing information about multiplicity is more informative than focusing on a single p-value. The sample-size illustrations also show how planning depends on the effect size one wants to detect, but they are not evidence about the study’s achieved power or its original design justification.

Finally, the registry gives a concrete example of how outcome availability and analysis populations can vary across visits and measures. Reading the results carefully means separating the primary endpoint from supplementary outcomes, sponsor analyses from simple recalculations, and serious-event counts from causal conclusions. Those distinctions are central to sound interpretation of clinical trial statistics.

19. Limitations

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

The registry record leaves important design and analysis details unavailable. It does not report the original sample-size justification, allocation ratio, allocation concealment procedure, interim analyses, or full statistical analysis plan. It also does not state whether multiplicity was controlled across the three primary dose comparisons and the several secondary outcomes. These omissions make it difficult to assess the results against the complete planned inferential framework.

The primary endpoint description specifies a repeated-measures model, while the sponsor analyses are labeled ANOVA. The record does not explain the relationship between those descriptions or provide enough detail to independently reproduce the sponsor estimates. The simple recalculations are unadjusted and differ from the sponsor p-values; because the record flags a discrepancy, they should not replace the sponsor’s results.

Available participant counts vary across outcomes and visits. The registry defines the primary analysis population but does not fully explain missing-data handling, imputation, assumptions about missingness, or sensitivity analyses. Arm descriptions are truncated, limiting assessment of the complete response-based treatment procedure. The registry also does not report a clinically important difference threshold for the primary endpoint.

The sample-size figures are illustrations based on observed effects rather than the original design. The safety record provides counts and selected serious-event terms but does not report deaths, exposure-adjusted rates, or enough context to attribute listed terms by treatment group. The posted secondary results cover only some of the outcomes listed. These constraints mean that conclusions should remain specific to the reported analyses and should not be extended to unreported outcomes or longer-term effects.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Dose Finding Study of Namilumab in Combination With Methotrexate in Participants With Moderate to Severe Rheumatoid Arthritis (RA) — NCT02379091.
• Registry record last updated 2018-09-14; status last verified 2018-08.
• Results first posted 2018-09-14.
• 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

The registry describes a completed randomized, double-blind, placebo-controlled, parallel-group phase 2 study of namilumab with methotrexate in participants with moderate to severe rheumatoid arthritis. Enrollment was 108. The primary outcome was change from Baseline in DAS28-CRP at Week 12, analyzed in a defined Full Analysis Set using a repeated-measures model.

The sponsor reported three dose comparisons with least-squares results, confidence intervals, and p-values. The record also includes selected secondary outcome summaries, planning illustrations based on observed effects, and serious adverse-event counts. Some outcomes and analysis details are absent, including the original sample-size justification, multiplicity procedures, and detailed missing-data methods.

A discrepancy is flagged between simple unadjusted recalculations and sponsor analyses; the sponsor’s results take precedence. The estimates and uncertainty should be interpreted as trial-specific statistical findings, not as clinical advice or proof of a universal effect.