Evaluation of the Efficacy and Safety of Sarilumab in Patients With Polymyalgia Rheumatica: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of the Efficacy and Safety of Sarilumab in Patients With Polymyalgia Rheumatica (NCT03600818), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Sustained Remission at Week 52.

2. Clinical Question

The trial addressed a treatment strategy rather than isolating the effect of sarilumab while keeping the prednisone schedule identical. The primary objective compared sarilumab alongside a shorter corticosteroid taper with placebo alongside a longer taper. That distinction matters: any contrast in outcomes belongs to these combined strategies as studied, and the primary endpoint does not separate the contribution of the drug from the contribution of the taper schedule.

The registry record describes a randomized, double-blind, placebo-controlled study in PMR. The listed primary outcome was the percentage of participants achieving sustained remission at Week 52. Other stated aims included clinical responses over time, cumulative corticosteroid exposure, safety and tolerability, serum concentrations, and glucocorticoid toxicity. The clinical question is therefore broader than the primary endpoint, but the primary result specifically addresses a composite set of remission, flare, CRP, and taper-adherence conditions.

3. Trial Design

The registry record describes NCT03600818 as a phase 3, randomized, quadruple-masked, parallel-group study sponsored by Sanofi. It lists 118 participants enrolled and PMR as the condition. The recorded study start was 2018-10-09, and primary completion was 2021-05-19. The current status is terminated; the reason for termination is not reported in the registry record.

The comparison involved two treatment strategies. Participants in the placebo group received sarilumab-matching placebo every two weeks and followed a 52-week prednisone taper. Participants in the sarilumab group received sarilumab 200 mg every two weeks and followed a 14-week prednisone taper. The intervention descriptions state that study injections could continue up to 52 weeks. Thus, the assigned groups differed in both the randomized biologic treatment and the corticosteroid taper duration. The registry’s result should be read as a comparison of those strategies, not as a drug-only contrast under the same taper.

The primary outcome was assessed at Week 52 in the intent-to-treat population. That population included participants allocated to a randomized group, analyzed according to the group assigned by randomization. The posted primary results include 58 participants in the placebo-plus-52-week-taper group and 60 in the sarilumab-plus-14-week-taper group. These are the group sizes for the primary outcome; safety figures use different at-risk counts for the sarilumab group.

The registry record lists secondary outcomes including cumulative corticosteroid dose, remission by Week 12, absence of flare from Week 12 through Week 52, sustained CRP reduction, prednisone-taper adherence, time to first flare after remission, glucocorticoid toxicity scores, and treatment-emergent adverse events. The original sample-size justification, planned interim analyses, and full statistical plan are not reported in the registry record. The reason for termination and any effect it had on conduct or analysis are also not reported in the registry record.

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 were randomized to two treatment groups in a 1:1 ratio by interactive response technology. A total of 118 participants were enrolled and randomized in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on intent-to-treat (ITT) population that included all participants who were allocated to a randomized treatment group, and were analyzed according to the treatment group allocated by randomization.

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: Analysis was performed on randomized population.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Sustained Remission at Week 52, measured over At Week 52.

The primary endpoint is the percentage of participants achieving sustained remission at Week 52. It is a binary outcome: each participant either meets the full definition or does not. The definition requires disease remission no later than Week 12, including resolution of PMR signs and symptoms and normalization of CRP to less than 10 mg/L. It also requires no disease flare from Week 12 through Week 52, sustained CRP below 10 mg/L without successive elevations to 10 mg/L or higher, and successful adherence to the prednisone taper during Week 12 through Week 52.

This endpoint is used to capture a sustained treatment outcome rather than a single improvement at one visit. Requiring the components together makes the endpoint clinically and analytically demanding: a participant who meets several components but fails another does not count as achieving the composite outcome. Because the components include symptoms, laboratory measures, flare, and taper adherence, the result reflects their joint occurrence under the trial’s definition.

The endpoint also aligns with the trial’s comparison of treatment strategies that used different corticosteroid taper schedules. It combines disease control with the ability to follow the assigned taper, rather than measuring symptom change alone. The registry record gives the definition and assessment time, but details of handling missing component measurements are not reported in the registry record.

7. Results Posted in the Registry

• Sarilumab 200mg q2w+14 Week Taper: 28.3% (17/60) versus 10.3% (6/58) on control; risk difference 18.0 percentage points (95% CI 4.2 to 31.8), risk ratio 2.74 (1.16–6.46); unadjusted two-proportion z-test p = 0.014.

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.

Total Cumulative Corticosteroid Dose

• 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:
  • Sarilumab 200mg q2w+14 Week Taper: mean 1,040 versus 2,236 on control; difference -1,196 (95% CI -1,463 to -929.71), standardized effect d = -1.63; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Sarilumab 200mg q2w+14 Week Taper than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Who Achieved Disease Remission up to Week 12

• 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:
  • Sarilumab 200mg q2w+14 Week Taper: 46.7% (28/60) versus 37.9% (22/58) on control; risk difference 8.7 percentage points (95% CI -9.0 to 26.5), risk ratio 1.23 (0.80–1.88); unadjusted two-proportion z-test p = 0.337.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sarilumab 200mg q2w+14 Week Taper and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Absence of Disease Flare From Week 12 Through Week 52

• 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:
  • Sarilumab 200mg q2w+14 Week Taper: 55.0% (33/60) versus 32.8% (19/58) on control; risk difference 22.2 percentage points (95% CI 4.8 to 39.7), risk ratio 1.68 (1.09–2.59); unadjusted two-proportion z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Sarilumab 200mg q2w+14 Week Taper than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary findings have a mixed pattern rather than a uniform early response across every measure. The posted remission count by Week 12 does not show clear evidence of a difference in the unadjusted comparison, while later absence of flare and cumulative corticosteroid dose favor the sarilumab-plus-shorter-taper group in their respective posted comparisons. These outcomes relate to different parts of the primary endpoint and treatment strategy: early remission, maintaining disease control, and corticosteroid exposure are not the same outcome.

The primary sustained-remission result requires several conditions to hold together. The secondary measures can help describe individual pieces of that composite, but they do not establish which piece drove the primary contrast. Nor should a result for one component be treated as proof that all components improved. Other listed outcomes include sustained CRP reduction, taper adherence, time to first flare, glucocorticoid toxicity scores, and adverse events. Numerical results for the remaining secondary outcomes are not reported in the registry record.

Unadjusted secondary results carry less weight because the registry lists multiple outcomes, and the record does not report whether the analysis plan controlled the overall chance of false-positive findings across them. A nominally small p-value among numerous tests may be less persuasive than a single prespecified primary comparison unless multiplicity is addressed. The registry record does not report a testing hierarchy or adjustment procedure.

Secondary outcomes can still be useful for context and for generating hypotheses. They should be read alongside their definitions, analysis methods, and uncertainty, rather than as a series of independent confirmations of the primary result. Differences in denominators or available observations may also matter; detailed missing-data handling for each secondary outcome is not reported in the registry record.

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

• Total Cumulative Corticosteroid Dose
• Number of Participants Who Achieved Disease Remission up to Week 12
• Number of Participants With Absence of Disease Flare From Week 12 Through Week 52
• Number of Participants With Sustained Reduction of CRP From Week 12 Through Week 52
• Number of Participants With Successful Adherence to the Prednisone Taper From Week 12 Through Week 52
• Time to First Polymyalgia Rheumatica Flare After Clinical Remission up to Week 52
• Composite Glucocorticoid Toxicity Index (C-GTI): Cumulative Worsening Score (CWS) and Aggregate Improvement Score (AIS) at Week 52
• Number of Participants With Treatment-emergent Adverse Events (TEAEs) and Treatment-emergent Serious Adverse Events (TESAEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary because each participant either met the sustained-remission definition or did not. A percentage summarizes the proportion meeting that definition in each randomized group. The registry’s primary analysis is identified as a Fisher exact test, with the effect expressed as a difference in percentage. Fisher’s exact test is a method for comparing binary outcomes between groups; it evaluates how compatible the observed allocation of outcomes is with a null hypothesis of no group association, given the group totals.

What does the difference estimate describe?

A risk difference compares the event proportions by subtraction, with the event defined as achieving sustained remission. A positive difference means the event proportion is higher in the sarilumab-plus-shorter-taper group than in the placebo-plus-longer-taper group. The sponsor reported the difference in percentage points. The simple unadjusted recalculation expresses the same comparison as a risk difference on a proportion scale. Those presentations use different scales, so the numerical forms should not be read as competing clinical outcomes.

The posted recalculation uses the observed binary outcomes and group sizes without adjustment for other variables. It reports a risk difference of 0.180 and an unadjusted p-value of 0.014. The registry’s reported analysis gives a difference in percentage of 18.0 and p = 0.019. The methods and presentation differ, so exact agreement is not expected. The registry record does not describe covariate adjustment for the primary comparison.

How should the confidence interval and p-value be understood?

A confidence interval gives a range of effect estimates compatible with the data under the method used, at the stated confidence level. It communicates uncertainty about the effect size as well as its direction. A p-value measures how unusual the observed data, or data more extreme, would be under a specified null hypothesis and analysis method. It is not the probability that the null hypothesis is true, and it does not measure the practical importance of the result. The registry’s primary confidence interval is reported at 95%.

The primary result is a group-level comparison under random allocation and the intent-to-treat analysis population. Intent-to-treat means participants are analyzed according to their randomized assignment, rather than being reassigned based on treatment received. This preserves the randomized comparison in the analysis definition. The registry record defines the primary population in this way, but detailed handling of missing Week 52 outcome data is not reported in the registry record.

Why can secondary methods differ?

The posted secondary result for total cumulative corticosteroid dose is a continuous outcome, reported as a mean and standard deviation in each group. Its simple recalculation estimates a mean difference of -1196.0 milligrams, with a confidence interval from -1463.0 to -929.7 and an unadjusted p-value of <0.001. The registry’s own analysis for that outcome is a Wilcoxon rank-sum test with p < 0.001. This rank-based method compares the distributions of observations using their ranks; it does not require the same modeling assumptions as a test of means. A test of means and a rank-sum test address related but not identical statistical questions, which can yield different p-values.

Other posted secondary outcomes are binary counts, such as remission by Week 12 and absence of flare during the later assessment period. Their unadjusted recalculations compare proportions between randomized groups. The registry record does not give a reported analysis for those two outcomes in the available result details. The methods for all remaining secondary endpoints are not reported in the registry record.

Statistical testing across multiple endpoints raises multiplicity concerns: as more hypotheses are tested, the chance of at least one apparently unusual result can rise if each is judged at the same threshold. The registry record lists 17 outcome measures and 2 analyses, but whether a hierarchical strategy, multiplicity adjustment, or other control was used is not reported in the registry record. Accordingly, unadjusted secondary p-values should not be treated as confirmatory evidence on their own.

For continuous outcomes, variability matters because the spread of individual observations affects the uncertainty around a group comparison. For binary outcomes, the number of events and participants in each group influence precision. These general statistical principles help explain why estimates can be uncertain even when their point estimates differ, and why the analysis population and missing-data approach matter. The registry record does not provide enough detail to assess all model assumptions or analysis decisions.

11. Confidence Intervals and Precision

The primary confidence interval reported by the registry is 4.15 to 31.82 for the difference in percentage, at the 95% confidence level. The interval is entirely above no difference, but it spans a range of possible magnitudes. It therefore supports a positive direction for the observed comparison under the reported method while leaving uncertainty about the size of the contrast. The unadjusted recalculation gives a risk-difference interval from 0.042 to 0.318, likewise above no difference. The sponsor’s reported analysis is the registry’s own primary analysis; the recalculation is supplementary.

Precision depends on the amount of information in the data, including the group sizes and the number of participants meeting the endpoint. The primary outcome counts were 6 of 58 in the placebo group and 17 of 60 in the sarilumab group. Because the endpoint is binary and the event counts are limited, the estimate should not be read as exact. The interval is more informative about uncertainty than the point estimate alone.

A confidence interval is not a range containing a known fixed percentage of individual participant outcomes, and it does not show which endpoint components were failed. It describes uncertainty in the estimated group contrast under the analysis method. It also does not account for every potential source of uncertainty, such as unreported missing-data procedures, unreported analysis choices, or limitations in generalizing beyond the randomized strategies.

For the secondary cumulative-dose comparison, the recalculated mean-difference interval is -1463.0 to -929.7 milligrams. This provides precision information for that outcome under its unadjusted calculation, while the registry’s reported rank-sum analysis uses a different method. Secondary estimates should be interpreted in the context of the full set of outcomes and the fact that multiplicity handling is not reported in the registry record.

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 trial’s original design calculations. For outcomes other than time-to-event outcomes, the figures are participants per arm; for time-to-event outcomes, they are total events. The primary endpoint is not a time-to-event outcome, so its planning figures are participants per arm.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column indicates the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect if that effect were present and the assumptions held. The 90% power column gives the corresponding planning figure for a 90% chance. These are design illustrations, not probabilities that the observed trial result is correct. The calculated figures are not observed power.

Smaller target effects require more participants because they are harder to distinguish from random variation. Thus, planning for a fraction of the observed effect produces larger sample-size requirements than planning for the full observed effect. The figures should be interpreted cautiously: they use an effect estimated from this trial’s posted results and assumptions that may differ from the original trial design. They do not demonstrate that the trial was adequately or inadequately powered, and they do not replace the confidence interval for understanding the precision of the observed result.

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 = 0.103; treatment proportion p₁ = 0.283; average p̄ = 0.193.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5586 = 1.0947.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5439 = 0.4577.
4. n = (1.0947 + 0.4577)² / (0.1799)² = 74.5, rounded up to 75 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 <- 0.103448275862069                          # control proportion
p1 <- 0.283333333333333                          # 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(3600818)
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 = 75 (80% power), 100 (90% power)
 75% of observed effect: n per arm = 122 (80% power), 162 (90% power)
 50% of observed effect: n per arm = 245 (80% power), 327 (90% power)
power.prop.test: 74.5 
Simulated power at n = 75 per arm: 0.816 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s own primary analysis used a Fisher exact test and reported a difference in percentage of 18.0, with a 95% confidence interval from 4.15 to 31.82 and p = 0.019. The simple unadjusted recalculation from posted group summaries gives a risk difference of 0.180, with a confidence interval from 0.042 to 0.318 and p = 0.014. Both comparisons point in the same direction, and both intervals exclude no difference. The reported estimates are close but are not identical because the recalculation and the registry analysis are distinct presentations and calculations.

The recalculation is an unadjusted check based on the posted counts; it does not replace the sponsor’s analysis or establish that the registry’s analysis was prespecified. The registry record does not report enough of the statistical plan to assess all analysis decisions. Since the record does not flag a discrepancy, the sponsor’s result can be described alongside the recalculation without asserting a conflict. The sponsor’s own reported analysis is the principal registry result for the primary endpoint.

For total cumulative corticosteroid dose, the registry reports a Wilcoxon rank-sum test with p < 0.001, while the recalculation estimates a mean difference and gives an unadjusted p-value of <0.001. These methods address the data differently, so the p-values should not be presented as interchangeable. The registry’s analysis is the posted sponsor analysis; the recalculated mean contrast is an additional descriptive comparison.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists multiple secondary outcomes, including several clinical, laboratory, corticosteroid-use, toxicity, and safety measures. Testing many outcomes creates a multiplicity issue: when each comparison is assessed separately, the chance of at least one result appearing statistically persuasive by chance can increase. A prespecified hierarchy or adjustment can address this concern, but whether either was used is not reported in the registry record. The available results therefore do not support treating every unadjusted secondary p-value as confirmatory.

The primary analysis population is described as intent-to-treat. Participants allocated to a randomized group were analyzed according to that assigned group. This helps preserve the randomized comparison and makes the estimand relate to assignment to the study strategies. The registry record does not report detailed rules for missing primary endpoint components, withdrawals, or incomplete follow-up. It is consequently not possible to assess from the record how missing observations were handled or whether sensitivity analyses were conducted.

The record does not report the full statistical analysis plan, the original sample-size justification, or interim analyses. It also does not report the reason for termination. These omissions leave uncertainty about whether the posted analysis follows a prespecified plan, whether any changes were made, and how termination affected the intended analyses. This is not evidence that a particular procedure was or was not used; the details are simply not reported in the registry record.

The available primary result should therefore be interpreted as the registry’s reported comparison for the defined intent-to-treat population, accompanied by the stated uncertainty. Secondary findings can add context, but their evidential weight is limited by unreported multiplicity control and missing analysis details. A registry record can describe outcome values and some methods without supplying every detail needed for a complete audit of statistical conduct.

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: covid-19 (3.4%), neutropenia (3.4%), covid-19 pneumonia (1.7%), alanine aminotransferase increased (1.7%), intervertebral disc protrusion (1.7%).

The safety figures use at-risk counts of 58 in the placebo-plus-52-week-taper group and 59 in the sarilumab-plus-14-week-taper group. Serious adverse events were recorded for 12 participants in the placebo group and 8 in the sarilumab group. Other treatment-emergent adverse events were recorded for 42 participants in each group. The registry reports no deaths in either group.

The listed serious adverse-event terms include Covid-19 and neutropenia, each reported as 3.4% in the sarilumab group, and Covid-19 pneumonia, alanine aminotransferase increased, intervertebral disc protrusion, and lumbar spinal stenosis, each reported as 1.7%. These are registry-listed terms and percentages; they do not establish that a study treatment caused an event.

These counts describe the posted safety results, not comparative risk-adjusted analyses. The registry record does not provide a full account of event duration, severity, relatedness assessments, exposure-adjusted rates, or detailed follow-up. The different safety denominator in the sarilumab group compared with the primary endpoint reflects that the outcome-specific populations differ; the record should be read using the denominator stated for each result. The figures alone do not establish the relative safety of the treatment strategies.

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

The posted primary result shows that a larger proportion of participants met the registry’s sustained-remission definition in the sarilumab-plus-14-week-taper group than in the placebo-plus-52-week-taper group. The registry’s own analysis reports a positive difference, with a 95% confidence interval above no difference. This is evidence about the comparison conducted in this trial, using the endpoint and treatment strategies defined in the registry.

It does not isolate sarilumab’s effect from the effect of the prednisone taper because the treatment groups had different taper schedules as well as different study injections. The result therefore concerns the combined strategies. It also does not mean that every participant in the sarilumab group achieved remission, or that participants who did not meet the endpoint had no improvement. The composite only records whether all required conditions were met.

The primary endpoint includes disease symptoms, CRP, flare, and prednisone-taper adherence. The result does not identify which of these components most influenced the group contrast. Nor does it describe every aspect of disease course or establish an effect on outcomes not measured by the trial. The separate secondary results provide context but are subject to their own definitions and uncertainty.

The confidence interval and p-value do not establish the exact magnitude or clinical importance of the difference. Statistical evidence against no difference is not the same as proof of a particular benefit, and the p-value is not the chance that the result occurred by luck or that the treatment strategy is ineffective. The interval expresses uncertainty under the reported method and does not resolve limitations in the record, including unreported missing-data procedures, multiplicity handling, and the reason for termination.

These results are not medical advice and do not determine what treatment is appropriate for an individual. They describe the registry’s randomized comparison and its posted outcome data, with the limitations of the combined intervention contrast and the information reported in the record.

18. Why This Trial Matters Statistically

This trial illustrates how the scientific question is shaped by the endpoint and the treatment contrast. Sustained remission was not defined as a single symptom score or laboratory value; it required several conditions across the study period, including adherence to a taper. That makes the outcome more comprehensive, but it also means the reported percentage cannot by itself reveal which component most affected the result.

The comparison also combines two treatment decisions: the randomized injection and the prednisone taper schedule. Statistically, randomization supports a comparison of the assigned strategies, but it does not disentangle effects of components that changed together. Clear interpretation therefore depends on describing the contrast accurately rather than attributing the entire difference to one component.

The registry provides both a sponsor-reported primary analysis and a simple unadjusted recalculation. Their estimates are close in direction and magnitude, while their p-values differ because the methods and calculations are not identical. This demonstrates why an independent summary calculation can be a useful check but should not displace the trial’s own analysis or be mistaken for a reconstruction of a full statistical plan.

The secondary outcomes show why evidence across endpoints needs a hierarchy. Measures of early remission, later flare, and cumulative corticosteroid exposure describe related but distinct aspects of the strategy. When many outcomes are assessed, unadjusted findings should be treated cautiously unless multiplicity procedures are reported. Missing statistical-plan and missing-data details further limit what can be concluded from registry results alone.

Finally, estimates and confidence intervals matter together. A point estimate gives a concise contrast, while the interval communicates uncertainty about its size. Reading both, alongside the endpoint definition, analysis population, and trial design, offers a more defensible statistical interpretation than relying on a p-value alone.

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 most important design-specific limitation is that sarilumab and placebo were paired with different prednisone taper schedules. The randomized comparison therefore estimates the contrast between sarilumab with a 14-week taper and placebo with a 52-week taper. It cannot separate the effect of the study injection from the effect of taper duration.

The primary endpoint is a composite requiring remission by Week 12, absence of flare, sustained CRP reduction, and successful prednisone-taper adherence through Week 52. A participant’s failure to meet any required component means the composite is not achieved. The registry’s primary result does not provide a breakdown of which components most often prevented sustained remission, so interpretation of the composite alone is limited.

The registry record labels the study terminated, but the reason and any consequences for enrollment, follow-up, or analysis are not reported in the registry record. The original sample-size justification and interim analyses are also not reported in the registry record. The posted enrollment and outcome counts do not, by themselves, explain whether the trial ended as planned or whether the termination affected precision.

Details about missing endpoint data, imputation, sensitivity analyses, and the handling of incomplete follow-up are not reported in the registry record. The statistical plan for multiplicity across the many listed outcomes is also not reported. These omissions make it difficult to assess the robustness of secondary findings and the full prespecification of analyses.

Finally, the primary endpoint is measured at Week 52 and summarizes a complex course into a binary outcome. It does not show the timing or severity of every flare, nor does it capture all possible patient outcomes. The findings apply to the randomized strategies and recorded outcomes in this trial; the registry record alone does not establish how results generalize to other treatment schedules or populations.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of the Efficacy and Safety of Sarilumab in Patients With Polymyalgia Rheumatica — NCT03600818.
• Registry record last updated 2022-06-10; status last verified 2022-05.
• Results first posted 2022-06-10.
• 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

NCT03600818 is a randomized, quadruple-masked, parallel-group phase 3 study in PMR, sponsored by Sanofi. The record lists 118 enrolled participants and a status of terminated. The reason for termination is not reported in the registry record.

The primary comparison was sarilumab 200 mg every two weeks with a 14-week prednisone taper versus sarilumab-matching placebo with a 52-week prednisone taper. At Week 52, sustained remission was recorded for 28.3% of the sarilumab group and 10.3% of the placebo group. The registry’s primary analysis reported a difference in percentage of 18.0, with a 95% confidence interval from 4.15 to 31.82 and p = 0.019.

The primary endpoint required remission by Week 12, no flare, sustained CRP reduction, and successful taper adherence through Week 52. The contrast is between combined treatment strategies, not sarilumab alone under a common taper. The registry record does not report the original sample-size justification, complete missing-data methods, multiplicity procedures, or the reason for termination.