Efficacy/Safety Study of Deferiprone Compared to Deferasirox in Paediatric Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy/Safety Study of Deferiprone Compared to Deferasirox in Paediatric Patients (NCT01825512), a randomized phase 3 study. The primary outcome is Percentage of Successfully Chelated Patients.

2. Clinical Question

In plain terms, the central question was whether the chelation-success result with deferiprone was sufficiently close to the result with deferasirox under a prespecified non-inferiority standard. A non-inferiority question is not the same as asking whether the two treatments are exactly equivalent. It asks whether any difference is small enough to meet a defined margin. Without the margin and the full endpoint decision rule, the registry’s summary does not allow readers to reconstruct the complete basis for a non-inferiority conclusion.

The outcome combines measures of iron burden, but their availability differs: serum ferritin was assessed in all patients, while cardiac MRI T2* was used only for patients above 10 years of age who could undergo MRI without sedation. That distinction matters when interpreting who contributed information to the composite endpoint. The registry does not report the detailed algorithm for combining these measures into a successful-chelation classification.

3. Trial Design

This was a phase 3, randomized, parallel-group, open-label, active-controlled trial. The registry lists an enrollment of 435 and identifies chronic iron overload as the condition. The study compared deferiprone with deferasirox in paediatric patients with transfusion-dependent haemoglobinopathies who required frequent transfusions and chelation. The planned treatment period in the brief summary was 12 months.

Random allocation means participants were assigned to study groups by a random process, rather than solely by clinician or participant choice. In general, randomization is intended to reduce systematic differences between groups at the point of assignment. The registry record does not report the randomization sequence method, allocation concealment procedures, or whether assignment was stratified.

The trial was open label, with no masking listed. Participants and study personnel therefore were not described as blinded to treatment assignment. In general, lack of masking can affect expectations, care decisions, and assessments that involve judgment. The primary endpoint includes laboratory and imaging measures, but the registry does not report whether endpoint assessors or analysts were masked.

The registry lists the trial as completed, with start and primary completion dates of 2014-03-17 and 2017-09-21. It does not report the original design assumptions or explain how the enrollment target was selected. A parallel-group design compares outcomes between groups receiving their assigned treatments over the same study period; details about adherence, treatment switching, and follow-up beyond the stated endpoint time are not reported in the registry record.

The primary outcome was recorded at baseline and after 12 months. Secondary measures included liver MRI, cardiac MRI T2*, and ferritin level. The record also reports adverse-event counts. These outcomes provide different kinds of information: a binary primary classification, continuous changes for secondary measures, and event counts for safety. Their distinct analysis populations and measurement scales should be kept in mind when comparing results.

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: Informed consent was collected for 435 patients that were enrolled in the study, however 42 of them were excluded from the study for the following reasons: 17 did not meet inclusion criteria, 5 withdrew the consent and 20 were lost to follow-up.

Baseline

Treatment

Analysis population for the primary outcome, as defined in the registry: Per-protocol population 1 (PP1): number of patients for whom the primary composite efficacy endpoint data were available at baseline and after 1 year of treatment (271 subjects)

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Successfully Chelated Patients, measured over at baseline and after 12 months.

The primary endpoint is the percentage of successfully chelated patients at baseline and after 12 months. The registry describes its assessment as based on serum ferritin levels in all patients and cardiac MRI T2* in patients above 10 years of age who were able to undergo an MRI scan without sedation. The primary population is per-protocol population 1: patients for whom primary composite efficacy endpoint data were available at baseline and after 1 year of treatment. The registry reports this population as 271 subjects.

For the posted counts, success is represented as a binary outcome: each contributing participant is classified as a success or not, and the group counts describe how many participants had the event of interest. The registry lists 69 successes among 125 participants in the deferiprone group and 80 among 146 in the deferasirox group. The reported outcome title uses “percentage,” while the posted arm values are counts. The record does not provide a detailed definition of the success threshold, explain how the two assessment components were combined, or state how missing components were handled.

Why use this endpoint? In general, a composite classification can condense multiple clinical measurements into an outcome that is easier to compare between groups. The underlying measures may nevertheless reflect different aspects of iron burden and may not be available for every participant in the same way. The age and MRI eligibility restriction is therefore relevant to interpretation: the endpoint was not based on identical measurement availability for all patients. The posted summary does not describe the component-level contributions to the successful-chelation classification.

7. Results Posted in the Registry

• Deferasirox: 54.8% (80/146) versus 55.2% (69/125) on control; risk difference -0.4 percentage points (95% CI -12.3 to 11.5), risk ratio 0.99 (0.80–1.23); unadjusted two-proportion z-test p = 0.947.

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.

Liver MRI

• 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:
  • Deferasirox: mean -2.98 versus -0.85 on control; difference -2.13 (95% CI -4.44 to 0.18), standardized effect d = -0.35; z-test p = 0.071.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferasirox and the control. The interval gives the range of effects that remain compatible with the data.

Cardiac MRI T2*

• 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:
  • Deferasirox: mean 1.12 versus 0.49 on control; difference 0.63 (95% CI -2.77 to 4.04), standardized effect d = 0.07; z-test p = 0.715.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferasirox and the control. The interval gives the range of effects that remain compatible with the data.

Ferritin Level

• 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:
  • Deferasirox: mean -398.18 versus -397.58 on control; difference -0.60 (95% CI -323.08 to 321.87), standardized effect d = -0.00; z-test p = 0.997.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferasirox and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the broad pattern is one of uncertain between-group differences rather than a consistent, clearly separated signal across measures. The recalculated confidence intervals span zero for the comparisons, while the sponsor-reported p-values do not indicate a clear statistical separation. These findings are secondary to the primary non-inferiority question and should not be used to replace it.

The secondary outcomes provide complementary information about iron burden: liver MRI, cardiac MRI T2*, and ferritin level do not measure precisely the same feature. They also have different analysis populations and data availability. In general, concordant results across distinct measures can help contextualize a primary endpoint, while differences across measures can arise from their different measurement properties, populations, and precision. The posted summaries do not provide component-level explanations that would establish why any observed patterns differ.

Unadjusted secondary findings carry less weight because multiple outcomes create multiple opportunities for apparently notable results. If many hypotheses are tested, some results may appear unusual by chance even when no real differences exist. The registry does not report a multiplicity adjustment or a prespecified hierarchy for secondary analyses. The secondary p-values should therefore be treated as exploratory evidence, not as independent confirmatory conclusions.

The secondary findings also do not resolve the main limitation in interpreting the primary outcome: the registry does not provide the non-inferiority margin or complete primary confidence interval. Nor do they establish equivalence between treatments. Their most defensible role is to add context about the posted measurements while recognizing their uncertainty, the differing sample availability, and the lack of reported multiplicity control.

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

• Liver MRI
• Cardiac MRI T2*
• Ferritin Level

9. Statistical Interpretation

10. Statistical Methods Explained

In general, a risk difference compares the proportion with an outcome in one group with the proportion in the reference group. A value near zero indicates that the observed proportions are close; the sign indicates which group has the higher observed proportion according to the chosen subtraction order. The re-calculation uses the posted counts for successful chelation and is unadjusted. It does not reproduce any covariate-adjusted or model-based analysis that may have been used by the trial investigators.

What does an unadjusted comparison represent?

An unadjusted comparison uses the group outcomes as recorded, without controlling statistically for other participant characteristics. Randomization is intended to make groups comparable on average, but the unadjusted estimate still reflects the particular participants and measurements observed. A re-calculation from summary counts is useful as a transparent check of the basic comparison, but it cannot reconstruct the trial’s full analysis dataset, endpoint programming, or handling of missing data.

The registry also reports a non-inferiority analysis for the primary endpoint. In general, non-inferiority analyses assess whether the result excludes an unacceptable loss relative to a prespecified margin. The margin, its rationale, the direction convention, and the complete primary confidence interval are not reported in the registry record. A reader cannot determine the non-inferiority decision from the lower confidence bound alone when the other required details are absent.

How should the continuous secondary outcomes be read?

The registry posts mean changes for liver MRI, cardiac MRI T2*, and ferritin level, with standard errors. A mean change summarizes the average change in a measured quantity among the participants included in that outcome. A mean difference compares the average changes between groups. The re-calculated comparisons are unadjusted; the registry’s own analyses use ANCOVA for the MRI outcomes and GLM for ferritin, as recorded. These model-based analyses are not identical to an unadjusted comparison of the posted summary statistics.

In general, ANCOVA compares outcome values while accounting for a baseline measurement or other specified covariates. A generalized linear model can represent an outcome using a chosen link and distribution, depending on its form. The registry does not list the covariates, model link, distribution, or other detailed specifications. Those details are needed to fully reproduce or assess a model-based result. The record labels the posted sponsor analyses but does not provide enough method detail to infer what adjustments were made beyond the named approach.

Why do confidence intervals matter?

A confidence interval describes a range of effect estimates compatible with the data and analysis procedure, under the assumptions of that procedure. It conveys precision as well as direction. An interval that includes zero for a difference is compatible with no difference, but it can also include differences in either direction. It is not a probability statement that the true effect lies within the specific interval, and it does not by itself establish equivalence or non-inferiority.

The confidence intervals for the recalculated comparisons are derived from the posted summary data and should be read as simple, unadjusted estimates. The sponsor’s model-based intervals may differ because the methods and possibly the analysis populations or covariates differ. The registry record does not report enough detail to reconcile all such differences analytically. The discrepancy indicator is false, so the record does not flag a discrepancy requiring the sponsor’s result to take precedence over the recalculation.

What is the role of the p-value?

A p-value evaluates how unusual data at least as different as those observed would be under a specified null model, assuming the model and analysis conditions hold. It does not measure the size or clinical importance of an effect, and it is not the probability that the null hypothesis is true. The posted unadjusted p-values are best considered alongside the effect estimates and confidence intervals, rather than as standalone verdicts.

The registry does not report whether the primary analysis used one-sided or two-sided testing, how its non-inferiority hypothesis was operationalized, or whether interim analyses were planned or conducted. These elements are not inferred from the posted p-values or study label. For the secondary endpoints, the registry posts model-based p-values, but does not report a multiplicity adjustment. As a general matter, testing several outcomes without accounting for multiplicity increases the chance of at least one apparently notable result arising by chance.

Why can over-dispersion matter?

General statistical context: for count or binary outcomes, a model may assume a particular level of variability. Over-dispersion means the observed variability exceeds that assumption. If present and not handled, standard errors can be too small and confidence intervals too narrow, making results appear more precise than warranted. The primary endpoint is posted as participant counts, but the registry does not report a model specification that would allow assessment of over-dispersion or identify whether it was relevant to the sponsor’s analysis.

Finally, data availability is part of the method, not merely a reporting detail. The primary endpoint population requires measurements at baseline and after 1 year. The registry does not report the missing-data method, the reasons for unavailable observations, or sensitivity analyses. General practice is to assess whether conclusions are robust to plausible assumptions about missing outcomes; whether such analyses were undertaken is not reported in the registry record.

11. Confidence Intervals and Precision

The recalculated primary risk-difference interval extends across zero, so the posted data are compatible with a range of possible group differences, including little or no difference and differences in either direction. Its unadjusted p-value is 0.947. This indicates that the observed counts do not provide a clear distinction under an ordinary test of difference, but the interval is the more informative guide to the range and precision of estimates compatible with the data.

A confidence interval is not a guarantee that the true effect falls inside its endpoints. In general, it is generated by a procedure that would cover the target effect at the stated rate over repeated applications, if the model assumptions hold. A wide interval indicates less precision; a narrow interval indicates greater precision. For a non-inferiority question, precision must be considered against the chosen margin, and the margin is not reported in the registry record. The reported primary analysis also lacks an upper confidence bound in the registry summary.

The secondary outcome intervals are also broad relative to their point estimates, and the recalculated intervals for those comparisons include zero. This means the posted summaries do not pin down a precise between-group difference for these outcomes. The estimates should not be interpreted as proof of no effect: uncertainty may include effects in more than one direction. Conversely, a point estimate alone does not establish a reliable difference.

Precision is affected by the number of observations and by variation in the measured outcome. The MRI outcomes have fewer observations than the primary endpoint population, and MRI eligibility was restricted for the primary composite measure. The registry does not report why observations were unavailable or provide detailed missing-data analyses. Those limits make it difficult to judge whether the observed precision reflects only sample size and variability or is also affected by selection into the endpoint 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 non-time-to-event outcomes in this trial; they are not total event counts. The registry’s planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers planning for 100%, 75%, or 50% of that observed effect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column gives the illustrative participants per arm for a design with an 80% chance of detecting the stated effect under the listed assumptions, if that effect and assumptions are correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design calculations, not guarantees about results. They also do not show the probability that the trial’s conclusion is correct.

The table illustrates a general relationship: smaller effects require more participants to detect, all else equal. The requirement can become particularly large when the observed effect used as a planning reference is very small. The figures are therefore sensitive to the effect assumption and should not be treated as a recommendation or as the trial’s planned enrollment target.

This is not observed power. Observed power is not an additional measure of evidential strength after results are known; the estimates and their uncertainty are more informative. The illustrations are conditional planning scenarios, not a retrospective claim about the probability that the completed trial would detect an effect.

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 = 0.552; treatment proportion p₁ = 0.548; average p̄ = 0.550.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7036 = 1.3790.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7036 = 0.5921.
4. n = (1.3790 + 0.5921)² / (-0.0041)² = 236,307.7, rounded up to 236,308 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 <- 0.552                          # control proportion
p1 <- 0.547945205479452                          # 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(1825512)
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 = 236,308 (80% power), 316,349 (90% power)
 75% of observed effect: n per arm = 420,018 (80% power), 562,284 (90% power)
 50% of observed effect: n per arm = 944,844 (80% power), 1,264,877 (90% power)
power.prop.test: 236307.7 
Simulated power at n = 236,308 per arm: 0.800 (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 is labeled non-inferiority and reports a treatment success rate of -12.5 with a 95% confidence interval lower bound of -12.5. It does not list an upper bound, a p-value, or the method used for this primary analysis. The non-inferiority margin is also not reported in the registry record. Those omissions prevent an independent assessment of whether the reported interval met the trial’s decision criterion.

The recalculated primary comparison uses the posted group counts and is an unadjusted risk difference. It is not a substitute for the sponsor’s intended analysis, especially when the endpoint definition, non-inferiority margin, and full model details are unavailable. The comparison should be read as a transparent arithmetic summary of the posted counts rather than as a reproduction of the sponsor’s inferential procedure.

For secondary outcomes, the sponsor analyses are identified as ANCOVA for the MRI measures and GLM for ferritin, with estimates, confidence intervals, and p-values listed. Recalculated comparisons from the posted means are unadjusted. Model-based and unadjusted estimates can differ because they answer slightly different statistical questions or use different adjustments. The registry does not report enough detail to explain the specifications fully. The discrepancy indicator is false; there is no flagged discrepancy requiring the sponsor’s own analysis to take precedence over the recalculations.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and several secondary outcomes, but does not report a multiplicity adjustment, a testing hierarchy, or a detailed statistical analysis plan. Multiplicity arises when multiple hypotheses are tested: even if every null hypothesis were true, the chance of at least one false-positive result can increase as the number of tests grows. General approaches include controlling the family-wise error rate or the false discovery rate, or designating some analyses as exploratory. Which approach, if any, was used is not reported in the registry record.

The registry identifies a non-inferiority analysis for the primary endpoint, but the non-inferiority margin is not reported. The method, direction convention, and full confidence interval are also absent from the primary analysis listing. A non-inferiority conclusion depends on those elements, so the summary does not permit a complete review of the decision rule. The registry does not report interim analyses, stopping rules, or the rationale for the original sample-size design.

The primary efficacy population is per-protocol population 1, defined by availability of primary composite endpoint data at baseline and after 1 year. The registry does not report a corresponding intention-to-treat analysis, reasons for missing data, treatment adherence, or the method used to handle missing endpoint components. This matters because a per-protocol analysis can exclude participants after randomization, and the selection may affect comparability if it is related to outcome or treatment experience. This is a general concern, not evidence that a particular bias occurred in this trial.

The registry also does not explain how MRI availability affected the primary composite outcome or how unavailable MRI or ferritin data were incorporated. The endpoint includes MRI only for patients above 10 years of age able to undergo scanning without sedation, while ferritin was assessed in all patients. Sensitivity analyses under alternative missing-data assumptions are not reported in the registry record. Without these details, the robustness of the primary finding to missingness and analysis-population choices cannot be assessed from the posted summary alone.

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 4% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: agranulocytosis (1.6%), neutropenia (1.0%), hypertransaminasaemia (1.0%), pneumonia (1.0%), sickle cell anaemia with crisis subjects affected/exposed (1.0%).

The registry lists serious adverse events for 13 of 193 at risk in the deferiprone group and 14 of 197 at risk in the deferasirox group. It lists other adverse events for 152 of 193 and 89 of 197 at risk, respectively. The record lists 0 deaths in each group. These are descriptive counts; they do not by themselves establish that an event was caused by a study treatment or indicate whether the groups differ reliably.

The listed serious-event terms include agranulocytosis at 1.6%, and neutropenia, hypertransaminasaemia, pneumonia, sickle cell anaemia with crisis, and chest pain at 1.0% each. The registry does not provide event-specific denominators or explain whether these terms refer to participants, event episodes, or another reporting unit in the displayed list. The terms should therefore be read as registry safety listings, not as comparative risk estimates.

The safety populations differ from the primary per-protocol endpoint population. The registry does not explain the basis for the safety denominators or provide exposure-adjusted event rates, event timing, severity distributions, or detailed causality assessments. Counts can be affected by the length of observation and by how events are collected. The posted figures are useful for describing reported events, but do not support a causal or definitive comparative safety conclusion on their own.

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

The posted primary counts and unadjusted comparison show similar observed chelation-success results in the two groups, with substantial uncertainty around the between-group estimate. The registry’s own analysis is labeled non-inferiority, but the summary lacks the margin and complete primary interval needed to independently verify the non-inferiority decision. The results therefore describe the observed trial data without establishing that the treatments are equivalent or that either is superior.

Failure to show a clear difference is not proof that there is no meaningful difference. A non-significant p-value can occur when effects are small, when estimates are imprecise, or both. A confidence interval helps distinguish these possibilities, but its interpretation for non-inferiority requires comparison with a prespecified margin. That margin is not reported in the registry record.

The findings apply to the populations and measurements recorded, including the primary per-protocol population with endpoint data at baseline and after 1 year. They should not automatically be generalized to all paediatric patients with haemoglobinopathies, to different treatment regimens, or to durations beyond the 12-month treatment period. The registry does not report enough detail about missing data, adherence, and endpoint construction to determine how those factors affect generalizability.

The secondary outcomes add context but are not decisive evidence on their own. They use different measurement scales and analysis populations, and no multiplicity adjustment is reported. Likewise, adverse-event counts are descriptive and do not establish treatment causation. The record supports a careful account of what was observed and how uncertain the comparisons are; it does not support medical advice or a claim that one regimen should be chosen over the other.

18. Why This Trial Matters Statistically

This trial illustrates why a non-inferiority label alone does not settle the interpretation of a result. Non-inferiority depends on a clearly specified margin, an appropriate analysis population, and a complete comparison interval. Although the registry identifies the primary analysis as non-inferiority, the margin and upper confidence bound are not reported. Readers therefore need to distinguish the stated trial objective from what can be independently verified in the posted summary.

It also demonstrates the difference between a treatment’s observed group results and a statistical conclusion. The posted counts produce an unadjusted comparison that is close to zero, but uncertainty remains. Neither the point estimate nor a p-value alone answers whether any possible difference is acceptably small. That requires a decision framework specified before the results are known.

The endpoint design brings together serum ferritin and cardiac MRI T2*, but MRI eligibility is restricted. Composite outcomes can be practical, yet their interpretation depends on how components are combined and what happens when a component is unavailable. Those rules are not reported in the registry record. Explicit endpoint definitions and transparent missing-data procedures are essential for reproducibility.

Finally, the trial provides a useful setting for separating confirmatory primary evidence from secondary and safety summaries. Several secondary measures and adverse-event listings can enrich interpretation, but their multiplicity, differing populations, and descriptive nature affect the weight they can carry. Clear reporting of analysis plans, uncertainty, and population definitions is as important as reporting the estimated effects.

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.

Several trial-specific reporting gaps limit interpretation. The registry does not report the non-inferiority margin, the rationale for choosing it, or the complete primary confidence interval. The primary analysis method and p-value are also absent. As a result, the stated non-inferiority objective cannot be independently assessed using the primary analysis listing alone.

The endpoint’s full classification rule is not reported. Although the record identifies serum ferritin and cardiac MRI T2* as assessment components, it does not explain the thresholds for success, how components were combined, or how missing component data were handled. MRI was limited to patients above 10 years of age who could undergo scanning without sedation, so the composite’s measurement availability was not uniform.

The primary analysis population is per-protocol population 1, defined by data availability at baseline and after 1 year. The record does not report why participants were outside this population, whether they completed assigned treatment, or a corresponding intention-to-treat result. It also does not provide missing-data sensitivity analyses. These gaps make it difficult to evaluate selection effects or the robustness of the primary result.

For the sponsor’s secondary analyses, the record names ANCOVA and GLM but does not provide full model specifications, covariates, or distributional details. Multiplicity handling is not reported, and the original sample-size assumptions are not reported in the registry record. Safety listings lack event-specific denominators and detailed exposure or causality information. These are limits of the posted registry summary; they do not establish that the underlying trial analyses were inadequate.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy/Safety Study of Deferiprone Compared to Deferasirox in Paediatric Patients — NCT01825512.
• Registry record last updated 2021-05-04; status last verified 2017-10.
• Results first posted 2021-04-08.
• 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

NCT01825512 is a completed phase 3, randomized, open-label, parallel-group trial comparing deferiprone with deferasirox in paediatric patients with transfusion-dependent haemoglobinopathies and chronic iron overload. The registry lists an enrollment of 435 and a 12-month treatment period.

The primary endpoint was successful chelation, assessed using serum ferritin and cardiac MRI T2* for eligible patients. The primary analysis population was per-protocol population 1, with endpoint data at baseline and after 1 year. The posted group counts yield an unadjusted comparison close to zero, with an interval spanning zero; the registry’s own non-inferiority listing does not include the margin or a complete confidence interval.

Secondary outcomes cover liver MRI, cardiac MRI T2*, and ferritin. Safety listings include serious and other adverse events and 0 deaths in each group. The results are best interpreted as descriptive evidence with uncertainty: the registry summary does not provide enough information to independently verify the primary non-inferiority decision or to draw definitive comparative conclusions.