To Assess the Impact of Ferric Carboxymaltose Compared With Iron Sucrose in Chinese Subjects on Correcting Iron Deficiency Anaemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Assess the Impact of Ferric Carboxymaltose Compared With Iron Sucrose in Chinese Subjects on Correcting Iron Deficiency Anaemia (NCT03591406), a randomized phase 3 study. The primary outcome is Participants Achieving an Increase in Hb of at Least 2 g/dL at Any Time up to Week 8.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, open-label, parallel-group study comparing ferric carboxymaltose with iron sucrose in Chinese subjects with iron deficiency anaemia. The registry lists an enrollment of 371. Both study treatments were administered by intravenous injection or drip infusion. Masking was listed as none, so the record describes the trial as open-label rather than blinded.

The registry lists the study as completed. The recorded start date is 2017-07-03, and the primary completion date is 2019-02-25. The sponsor is Vifor (International) Inc. These record details describe the trial's administrative and design context; they do not establish how treatment was delivered at each site or how participants and investigators may have understood treatment assignment beyond the registry's open-label classification.

The primary endpoint was a binary outcome: whether a participant achieved an increase in haemoglobin of at least 2 g/dL at any time up to Week 8. The primary population was the Per Protocol Set, defined using randomization, treatment exposure, baseline and post-baseline measurements, treatment compliance, and protocol-violation criteria. The posted arm counts for this endpoint are 177 for FCM and 178 for IS, while the corresponding numbers achieving the endpoint are 176 and 175.

The registry also lists secondary outcomes involving haemoglobin, iron deficiency correction, transferrin saturation, serum ferritin, serum iron, treatment-emergent adverse events, and blood pressure. The record lists 12 outcome measures and 11 posted secondary outcomes. The detailed statistical plan, including the original sample-size justification, is 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: Subjects who provided signed and dated informed consent were screened within 7 days prior to initial treatment administration.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per Protocol Set: participants who were randomised, received at least 1 dose of study treatment, had at least 1 baseline and post-baseline value (Hb, ferritin, TSAT), had a study drug compliance between 80% and 120% and had no major protocol violations

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: Demography and baseline characteristics for the Safety Set (SS) are provided. The SS was defined as all randomised subjects who received at least 1 dose of study medication.

6. Primary Endpoint

The registry lists the primary outcome as Participants Achieving an Increase in Hb of at Least 2 g/dL at Any Time up to Week 8, measured over From baseline at any time up to Week 8.

The primary endpoint records whether each participant achieved an increase in haemoglobin of at least 2 g/dL from baseline at any time up to Week 8. It is a binary outcome: a participant either met this threshold during the stated period or did not. The registry identifies haemoglobin as the measurement and the Per Protocol Set as the analysis population.

A threshold-based outcome can express whether participants reached a specified response criterion, rather than describing the size of every participant's haemoglobin change. The posted counts therefore represent participants meeting the criterion, and the comparison concerns the proportions meeting it in the FCM and IS groups. This type of endpoint is useful for a treatment comparison framed around response, but it does not, by itself, describe the full distribution of haemoglobin changes or the timing of each response within the assessment period.

The endpoint's stated window extends from baseline to any time up to Week 8. The registry also lists secondary haemoglobin outcomes at Weeks 2, 4, 6 and 8, including change from baseline and achievement of an increase of at least 2 g/dL at those time points. Those repeated outcomes add distinct views of the response over time, but they are not interchangeable with the primary endpoint's any-time criterion.

The registry calls the primary comparison non-inferiority. Interpreting that claim requires the prespecified non-inferiority margin and the analysis rules used to apply it. The margin and full analysis rules are not reported in the registry record.

7. Results Posted in the Registry

• Iron Sucrose (IS): 98.3% (175/178) versus 99.4% (176/177) on control; risk difference -1.1 percentage points (95% CI -3.3 to 1.1), risk ratio 0.99 (0.97–1.01); unadjusted two-proportion z-test p = 0.317.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a binary endpoint comparison measure?

The primary outcome is binary because it classifies each participant according to whether the haemoglobin threshold was reached by the stated time. For this kind of outcome, the group-level quantity is the proportion meeting the criterion. The posted results give the counts meeting the endpoint and the analysis-set counts for both groups. Those counts are the basis for describing the observed proportions.

A risk difference expresses the difference between two proportions, with the sign depending on which group is subtracted from which. The recalculated contrast is stated as IS relative to FCM, so its negative estimate means the observed proportion was lower in IS than in FCM under that orientation. A risk difference close to zero indicates that the observed proportions are close on an absolute scale. The estimate remains uncertain, and the confidence interval describes a range of values compatible with the data and the calculation method.

What does the confidence interval add?

A confidence interval communicates uncertainty around an estimated contrast. It is not a guarantee that the true effect lies inside the particular interval, nor does it assign a probability to a fixed effect after the data have been observed. It helps readers judge both the direction and the range of effects consistent with the analysis. In the recalculation, the 95% interval includes zero, which is consistent with no difference under this unadjusted contrast, while also allowing values on either side of zero.

A confidence interval used for a difference test is not automatically a non-inferiority test. Non-inferiority requires a margin chosen in advance and a comparison of the interval with that margin in the direction that corresponds to the proposed claim. The margin and the sponsor's detailed decision rule are not reported in the registry record. Accordingly, the recalculated interval is informative about the unadjusted difference but cannot independently establish the registry's stated non-inferiority conclusion.

Why are the sponsor's and recalculated results distinct?

The registry reports the sponsor's result as a difference in proportions of 1.12, with a 95% confidence interval from -2.15 to 4.71. It does not report a p-value or a method for that analysis. The separate recalculation is an unadjusted estimate based on posted group counts, and its comparison is expressed as IS relative to FCM. The two results therefore need to be read according to their own reported orientation and analysis description; they should not be silently treated as identical methods or as a single estimate.

For a question about the sponsor's formal non-inferiority assessment, the sponsor's reported analysis is the relevant result. The recalculation is useful as a transparent check on the posted counts, but does not replace an analysis that may use prespecified procedures not detailed in the registry record. The registry's discrepancy indicator is false.

What does the p-value say?

The recalculated p-value is 0.317. Under the assumptions of the unadjusted difference test, it describes how unusual a result at least as incompatible with a no-difference model would be if that model were true. It is not the probability that the treatments are equal, and it is not the probability that the observed result occurred by chance. A p-value also does not establish equivalence or non-inferiority. Those claims require their own definitions and analysis criteria.

The sponsor's reported non-inferiority analysis has no p-value listed in the registry record. The absence of a posted p-value does not mean that none was calculated; it means the registry does not report one. Likewise, no unreported statistical test should be inferred from the confidence interval alone.

Why does the analysis population matter?

The primary endpoint is reported for the Per Protocol Set, not simply for everyone enrolled. The definition requires treatment receipt, relevant baseline and post-baseline measurements, a compliance range, and the absence of major protocol violations, in addition to randomization. Restricting the analysis in this way can make the reported contrast different from one based on all randomized participants. In non-inferiority trials, analysis populations and missing outcome handling can be especially consequential, but the registry record does not provide enough detail to evaluate those choices fully.

The record does not report the primary endpoint's missing-data method, the number excluded from the Per Protocol Set, or the corresponding intention-to-treat result. It also does not report whether sensitivity analyses tested alternative assumptions about missing outcomes or protocol deviations. These omissions limit assessment of how robust the primary comparison is to analysis-population choices.

What statistical details are not reported?

The registry record does not report the non-inferiority margin, the original sample-size justification, the detailed primary analysis method, adjustment factors, or interim-analysis plans. It does not state how multiplicity across secondary outcomes was handled. The posted result should therefore be interpreted using the information actually recorded: endpoint definition, analysis population, arm counts, sponsor estimate and interval, and the recalculated unadjusted comparison.

For general context, non-inferiority designs require a margin that is clinically and statistically justified before examining the result. A confidence interval's position relative to that margin determines whether the data meet the specified criterion. This general principle explains why the margin is essential, but it does not identify the margin used in this trial.

10. Confidence Intervals and Precision

The recalculated risk difference for IS relative to FCM is -0.011, with a 95% confidence interval from -0.033 to 0.011. The estimate lies close to zero, and the interval crosses zero. This indicates that the posted counts are compatible with a small difference in either direction under the unadjusted calculation. The interval does not establish that the treatments are equivalent, because equivalence requires defined bounds and a corresponding analysis.

The interval also cannot be used by itself to decide non-inferiority. The registry describes the sponsor's analysis as non-inferiority and reports a difference in proportions of 1.12, with a 95% confidence interval from -2.15 to 4.71. The non-inferiority margin is not reported in the registry record, and the statistical method for the sponsor's interval is not specified. Without the margin, the interval cannot be evaluated against the trial's intended non-inferiority criterion.

Confidence intervals generally show the precision of an estimate as well as its uncertainty. A narrower interval permits a more precise range of compatible values than a wider interval, but precision alone does not determine clinical importance. Here, the endpoint counts are near the top of the observed range, and the estimate is based on a binary threshold. The result therefore says specifically how the threshold proportions compare, not how the full haemoglobin response distributions compare.

The posted recalculation is unadjusted. The registry record does not report the details needed to assess whether the sponsor's analysis used additional prespecified features or how missing data were handled. The sponsor's reported interval and the recalculated interval should therefore be treated as separate summaries rather than as interchangeable measures of precision.

11. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design assumptions. For this binary outcome, the listed values are participants per arm, not total events. The planning 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 the stated fraction of the observed effect. The original sample-size justification is not reported in the registry record.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the specified effect under those planning assumptions, if that effect were the true one and the model assumptions held. The 90% power column gives the corresponding planning target for a 90% chance. These are design calculations, not a measure of how likely the trial's observed finding is to be true.

The rows distinguish planning for 100%, 75% and 50% of the observed effect. The figures are 1,391 and 1,861 participants per arm for 100% of the observed effect; 2,168 and 2,901 for 75%; and 4,191 and 5,609 for 50%, for 80% and 90% power respectively. Smaller effects require more participants to detect under the same assumptions, which is why the planned numbers increase as the target effect becomes a smaller fraction of the observed effect.

These calculations are not observed power. They are forward-looking illustrations that depend on the stated assumptions and effect-size choices. They do not show the probability that the primary result is correct, and they do not establish whether the trial's own design was adequately powered for its non-inferiority objective.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.994; treatment proportion p₁ = 0.983; average p̄ = 0.989.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1492 = 0.2924.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1490 = 0.1254.
4. n = (0.2924 + 0.1254)² / (-0.0112)² = 1,390.0, rounded up to 1,391 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 <- 0.994350282485876                          # control proportion
p1 <- 0.98314606741573                          # 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(3591406)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,391 (80% power), 1,861 (90% power)
 75% of observed effect: n per arm = 2,168 (80% power), 2,901 (90% power)
 50% of observed effect: n per arm = 4,191 (80% power), 5,609 (90% power)
power.prop.test: 1390 
Simulated power at n = 1,391 per arm: 0.822 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The registry reports the sponsor's primary analysis as a non-inferiority analysis of the difference in proportions. The reported estimate is 1.12, with a 95% confidence interval from -2.15 to 4.71. No p-value or analysis method is listed for this result. The non-inferiority margin is also not reported in the registry record, so the reported interval cannot be independently assessed against the criterion that would define non-inferiority.

The posted-count recalculation is a simple unadjusted risk difference, expressed as IS relative to FCM. It is -0.011, with a 95% confidence interval from -0.033 to 0.011 and p = 0.317. This calculation is useful for describing the contrast implied by the posted counts, but it is not the sponsor's formal analysis and does not reproduce unreported features of that analysis. The registry discrepancy indicator is false.

The sponsor's result should be used when describing the trial's reported non-inferiority analysis; the recalculation should be identified as an unadjusted check based on the posted counts. Because the registry does not provide the margin and full method, neither a reader nor a recalculation can independently reconstruct the sponsor's complete non-inferiority decision from the record alone.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is clearly identified as achievement of an increase in haemoglobin of at least 2 g/dL at any time up to Week 8. The registry also lists secondary outcomes involving haemoglobin responses and changes at Weeks 2, 4, 6 and 8, iron deficiency correction, transferrin saturation, serum ferritin, serum iron, treatment-emergent adverse events, and blood pressure. The record lists 12 outcome measures and 11 posted secondary outcomes.

Testing several outcomes or time points can increase the chance of at least one apparently noteworthy result if each is assessed without accounting for the others. General approaches to this issue include prespecifying a testing sequence, adjusting significance thresholds, or treating secondary findings as exploratory. Which approach, if any, was used for this trial is not reported in the registry record. The primary endpoint result should not be read as if it automatically resolves all the secondary comparisons.

The record does not report the full statistical analysis plan, an adjustment strategy for multiplicity, interim analyses, or a detailed hierarchy among secondary endpoints. It also does not report a missing-data method for the primary endpoint, the number excluded from the Per Protocol Set, or the result from an all-randomized analysis population. The primary analysis population definition is reported, but its construction and sensitivity to exclusions cannot be assessed from the available record.

These omissions matter because the primary analysis uses a per-protocol population and the trial is labelled non-inferiority. General statistical practice recognizes that non-inferiority conclusions can be sensitive to missing observations, protocol deviations, and analysis-population definitions. That general concern does not establish that a problem occurred in this trial; it identifies information needed to evaluate the robustness of the reported analysis.

The registry defines the Per Protocol Set as participants who were randomized, received at least 1 dose, had baseline and post-baseline values for haemoglobin, ferritin and transferrin saturation, had compliance between 80% and 120%, and had no major protocol violations. Further details about how these criteria were applied, and whether other analysis populations produced similar results, are not reported in the registry record.

15. 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 2.0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: crohn's disease (1.1%), menorrhagia (1.1%), abdominal adhesions (0.6%), adenomyosis (0.6%), pelvic adhesions (0.6%).

The registry reports serious adverse events for the safety groups separately from the primary endpoint analysis population. For FCM, 10 of 187 participants at risk were reported with a serious adverse event. For IS, 7 of 180 participants at risk were reported with a serious adverse event. The record reports 0 deaths in each group. These are counts and denominators as recorded; they are not the same group counts used for the primary Per Protocol Set outcome.

The registry lists serious-event terms and percentages including Crohn's disease at 1.1%, menorrhagia at 1.1%, abdominal adhesions at 0.6%, adenomyosis at 0.6%, pelvic adhesions at 0.6%, and anaphylactic shock at 0.6%. These terms are the listed leading serious-event terms, not a complete account of every possible safety outcome. The record also lists treatment-emergent adverse events among the secondary outcomes.

Counts of serious adverse events provide a descriptive safety summary. They do not, without further analysis, establish whether a treatment caused an event or whether the groups differ reliably in safety. The registry record does not report a comparative statistical analysis for these serious-event counts in the information available for the primary comparison. These figures should therefore be read as posted event counts and not as advice about treatment.

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

The posted primary result shows that 176 of 177 participants in the FCM Per Protocol Set and 175 of 178 in the IS Per Protocol Set met the haemoglobin response threshold by Week 8. The unadjusted recalculation gives a risk difference of -0.011 for IS relative to FCM, with a 95% confidence interval from -0.033 to 0.011 and p = 0.317. The observed proportions are close, while the interval reflects uncertainty around the contrast.

The registry identifies the sponsor's primary analysis as non-inferiority and reports a difference in proportions of 1.12, with a 95% confidence interval from -2.15 to 4.71. The non-inferiority margin and detailed analysis method are not reported in the registry record. Therefore, the posted information supports describing the trial's stated non-inferiority analysis and its reported estimate, but it does not allow an independent reader to verify the non-inferiority criterion.

The result is specific to a threshold response in the Per Protocol Set and a time window extending to Week 8. It does not summarize the magnitude of haemoglobin change for every participant, all iron laboratory measures, safety outcomes, or outcomes beyond the stated window. The registry lists secondary measures for several of these topics, but their findings are not captured by the primary endpoint alone.

Neither the close observed proportions nor a confidence interval that includes zero proves that the treatments are equivalent. Equivalence and non-inferiority are different claims from failure to detect a difference, and both require prespecified margins and suitable analysis rules. Those margins are not reported in the registry record. The result also does not establish that either treatment works or does not work; it describes the comparative data posted for this endpoint.

Safety findings should be considered separately. The serious-event counts and listed event terms are descriptive, and the available record does not provide a formal comparative safety analysis in this primary-results information. In combination, the endpoint and safety summaries offer bounded statistical descriptions, not a complete basis for clinical decisions.

17. Why This Trial Matters Statistically

This trial is statistically notable because the registry frames the primary objective as non-inferiority, while the posted primary endpoint is a binary response measure with very high observed proportions in both groups. In a non-inferiority analysis, the question is not simply whether the groups differ statistically. The analysis must determine whether the uncertainty around the contrast excludes an unacceptable loss, as defined by a prespecified margin.

The sponsor's reported estimate and confidence interval are available, but the margin and full method are not reported in the registry record. That distinction is important: an estimate near zero may appear reassuring as a descriptive comparison, yet it cannot establish non-inferiority without the benchmark specified for the trial. The unadjusted recalculation provides a transparent view of the posted counts, but does not fill in the missing design criterion.

The analysis population also matters. The primary endpoint is reported for a Per Protocol Set defined by treatment receipt, measurement availability, compliance, and protocol adherence. Such criteria are relevant to interpretation of a non-inferiority comparison because exclusions and missing observations can affect the contrast. The registry does not report the corresponding all-randomized result or the missing-data approach, leaving important robustness questions open.

More generally, this example distinguishes a descriptive similarity in observed proportions from a formal claim of non-inferiority. It also shows why a confidence interval, analysis population, margin, and analysis plan need to be read together. The posted result can be summarized accurately, but the missing methodological details limit how far the non-inferiority conclusion can be independently evaluated.

18. Limitations

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

The registry record does not report the non-inferiority margin, so the sponsor's interval cannot be assessed against the trial's stated criterion. The statistical method used for the sponsor's analysis is not specified, and no p-value is listed for that result. The original sample-size justification and the trial's own design assumptions are also not reported in the registry record; the available planning illustrations are based on the observed effect rather than the original design.

The primary endpoint is reported in the Per Protocol Set. The record defines that set but does not report the number excluded from it, the result for all randomized participants, or a sensitivity analysis using alternative analysis populations. The missing-data method for the primary endpoint is not reported. These details would help determine how exclusions, incomplete measurements, and protocol deviations may have affected the result.

The registry does not report the full statistical analysis plan, adjustment for multiplicity across secondary outcomes, or interim-analysis information. It lists secondary outcomes but does not, in the registry entries, provide their numerical results. Consequently, the primary endpoint cannot stand in for a complete assessment of haemoglobin trajectories, iron measures, or safety.

The trial is open-label, with masking listed as none. The registry record does not describe additional procedures that might reduce the influence of knowledge of treatment assignment on measurement or reporting. This is a design feature to consider, not evidence that bias occurred. The primary outcome uses a threshold and a time window through Week 8, so it also does not describe the size or persistence of haemoglobin changes beyond that criterion and period.

Finally, the serious adverse event counts are descriptive in the posted record. A detailed comparative safety analysis is not reported with the primary result. These limitations concern the information available in the registry record and do not imply that unreported analyses were not conducted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: To Assess the Impact of Ferric Carboxymaltose Compared With Iron Sucrose in Chinese Subjects on Correcting Iron Deficiency Anaemia — NCT03591406.
• Registry record last updated 2021-06-10; status last verified 2021-05.
• Results first posted 2020-05-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes NCT03591406, a completed phase 3 randomized, open-label, parallel-group study sponsored by Vifor (International) Inc. It compared intravenous ferric carboxymaltose with intravenous iron sucrose in Chinese subjects with iron deficiency anaemia. The recorded study start date is 2017-07-03, and the primary completion date is 2019-02-25. Enrollment is listed as 371.

The primary outcome was achievement of a haemoglobin increase of at least 2 g/dL at any time up to Week 8 in the Per Protocol Set. The posted counts were 176 of 177 for FCM and 175 of 178 for IS. The recalculated unadjusted risk difference for IS relative to FCM was -0.011, with a 95% confidence interval from -0.033 to 0.011 and p = 0.317. The sponsor's reported non-inferiority estimate was 1.12, with a 95% confidence interval from -2.15 to 4.71.

The non-inferiority margin, detailed analysis method, missing-data approach, and original sample-size justification are not reported in the registry record. The posted primary counts describe similar observed proportions, but the available record does not permit independent verification of the formal non-inferiority criterion.