Study to Test the Hypothesis of Non-inferior Efficacy and Safety of Ferrum Lek® (Iron (III) Hydroxide Polymaltosate), 100 mg Chewable Tablets (Lek d.d., Slovenia), as Compared With MALTOFER® (Vifor S.A., Switzerland), in Subjects With Mild and Moderate Iron Deficiency Anemia.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Test the Hypothesis of Non-inferior Efficacy and Safety of Ferrum Lek® (Iron (III) Hydroxide Polymaltosate), 100 mg Chewable Tablets (Lek d.d., Slovenia), as Compared With MALTOFER® (Vifor S.A., Switzerland), in Subjects With Mild and Moderate Iron Deficiency Anemia. (NCT03993288), a randomized phase 3 study. The primary outcome is Change From Baseline in Blood Hemoglobin Level (g/L).

2. Clinical Question

The trial compared two active treatments containing iron (III) hydroxide polymaltosate. Its primary outcome was a continuous measurement: the change in blood hemoglobin level, expressed in g/L, from baseline to Week 12. The registry describes the objective as a non-inferiority comparison rather than a test that the treatments are exactly equal.

In a non-inferiority study, the question is whether the result for the treatment under study is not worse than the comparator by more than a prespecified clinically acceptable margin. The margin and its justification are essential to interpreting that question. Neither is reported in the registry record. The posted non-inferiority analysis can therefore be described, but the threshold that it was meant to evaluate cannot be checked from the record.

The comparison is between treatment groups under the study conditions, not a comparison of either treatment with no treatment. The registry record identifies randomization and an open-label design. It does not report the allocation ratio or the details of how randomization was implemented. The primary outcome population also has a specific data requirement: participants needed at least one dose and hemoglobin measurements both before and after treatment. That definition matters when relating the analysis to the randomized study population.

3. Trial Design

This was a phase 3, randomized, parallel-group, open-label, active-controlled study. The record describes the condition as mild and moderate iron-deficiency anaemia and lists Sandoz as the sponsor. The study status is completed. The recorded start date was 2019-06-27, and the primary completion date was 2020-06-18. Enrollment was 267.

Participants were assigned to Ferrum Lek or MALTOFER. Both regimens were 100 mg chewable tablets of iron (III) hydroxide polymaltosate, taken as 2 tablets daily (200 mg) for 12 weeks. The trial therefore compared two named products using the same stated daily dose and treatment duration. It did not include a placebo group according to the listed interventions.

Open-label means the study was not masked. Knowledge of assigned treatment can affect aspects of trial conduct and outcome assessment, particularly when outcomes involve judgment. Hemoglobin is a laboratory measurement, but the record does not report whether laboratory staff or other personnel were masked to treatment assignment. Details about random-sequence generation, allocation concealment, site count, eligibility criteria, and adherence procedures are not reported in the registry record.

The primary outcome was change from baseline in blood hemoglobin level at Week 12. The stated primary population was the intention-to-treat population, defined in the record as randomized participants who received at least one dose and had hemoglobin data before and after treatment. Thus, the named population does not include every randomized participant regardless of whether outcome data were available. The record reports arm-level analyzed counts of 123 for Ferrum Lek and 129 for MALTOFER for the primary outcome. The analysis details do not explain how missing measurements or protocol deviations were handled.

The study also listed changes in serum iron, transferrin, percent transferrin saturation, and ferritin, as well as the number of participants with response to therapy. The listed outcomes do not by themselves establish how the study controlled false-positive findings across multiple endpoints. That approach 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: Participants were randomized in 1:1 ratio to two treatment arms.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-to-treat (ITT) population included all randomized participants who were administered at least one dose of the investigational product or comparator and who had hemoglobin level data both before and after treatment with the investigational product and the reference product.

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 Change From Baseline in Blood Hemoglobin Level (g/L), measured over Baseline and Week 12.

The primary endpoint is change from baseline in blood hemoglobin level, measured in g/L, at Week 12. It compares the Week 12 hemoglobin measurement with the baseline value for each participant, then summarizes change within each treatment group and compares the groups. The registry describes the outcome as a mean with standard deviation and frames the group comparison as non-inferiority.

Hemoglobin is a continuous laboratory measure, so a mean change provides a group-level summary of the direction and size of observed change. The standard deviation describes how much individual participants’ changes vary around the group mean. These are different quantities: the mean describes the average change, while the standard deviation describes spread among participants.

Using a prespecified primary endpoint helps focus the main comparison and reduces the risk that interpretation is driven by whichever outcome happens to look most favorable. In a non-inferiority study, however, the mean difference alone is not sufficient to determine whether the objective was met. Interpretation also depends on the chosen non-inferiority margin, the direction of the comparison, the confidence interval, and the analysis population and method.

The record identifies the baseline value as the screening visit and the endpoint assessment as Week 12 after 12 weeks of treatment. The exact timing rules, handling of measurements outside the target visit window, and any imputation for missing data are not reported in the registry record.

7. Results Posted in the Registry

• MALTOFER: mean 18.52 versus 18.33 on control; difference 0.19 (95% CI -3.47 to 3.85), standardized effect d = 0.01; z-test p = 0.919.

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.

Number of Participants With Response to the Therapy

• 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:
  • MALTOFER: 43.4% (56/129) versus 48.0% (59/123) on control; risk difference -4.6 percentage points (95% CI -16.8 to 7.7), risk ratio 0.91 (0.69–1.19); unadjusted two-proportion z-test p = 0.468.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between MALTOFER and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists five secondary outcomes: changes in serum iron, transferrin, percent transferrin saturation, and ferritin, along with the number of participants with response to therapy. A numerical comparison is posted for the response outcome. Detailed numerical results for the other listed secondary outcomes are not reported in the registry record.

These measures address related but distinct aspects of the study. The laboratory changes are continuous outcomes, while response is a participant classification. They can provide context alongside the primary hemoglobin endpoint, but they do not replace the primary comparison or resolve uncertainty about the non-inferiority margin and sponsor analysis. The registry record does not support a conclusion about an overall pattern across all five secondary outcomes because complete results are not reported for them.

Secondary results generally carry less evidential weight than a prespecified primary analysis, especially when many outcomes are considered. Testing multiple outcomes creates more opportunities for chance findings. The record does not report whether secondary analyses followed a prespecified hierarchy, whether multiplicity was controlled, or whether results were treated as exploratory. The response outcome’s unadjusted comparison should therefore be interpreted as one secondary result rather than independent confirmation of the primary result.

The response definition is not reported in the registry record. Without that definition, readers cannot assess the clinical or operational criteria used to classify participants as responders. Missing-data handling for the secondary outcomes is also not reported. These limitations constrain interpretation of the secondary evidence beyond the specific numbers posted for the response endpoint.

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

• Change From Baseline in Serum Iron
• Change From Baseline in Transferrin
• Change From Baseline in Percent Transferrin Saturation
• Change From Baseline in Ferritin
• Number of Participants With Response to the Therapy

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, and the record summarizes it using group means and standard deviations. A mean is the arithmetic average of observed changes within a group. A standard deviation describes the spread of those changes around the mean. The mean difference compares the two group averages. Its sign depends on the order of subtraction, so the contrast used for any estimate should be checked before describing which group has the numerically larger change.

The recalculated primary comparison is an unadjusted comparison based on the posted arm summaries. It reports the group means, standard deviations, sample counts, and an estimated mean difference with a confidence interval and unadjusted p-value. It does not adjust for baseline values or other participant characteristics. It is distinct from the registry’s sponsor-reported ANCOVA, which is an adjusted analysis method. The covariates and model details used in that ANCOVA are not reported in the registry record.

What does a confidence interval describe?

A confidence interval gives a range of values compatible with the observed data under the assumptions of the analysis. It conveys uncertainty around an estimated effect; a wider interval indicates less precision than a narrower interval on the same scale. It is not a range containing every participant’s result, nor does it assign a probability to a particular effect being true. A confidence interval must be interpreted in relation to the question being asked and, for non-inferiority, the prespecified margin.

The registry reports a 95% confidence interval for the sponsor analysis and the recalculation. The sponsor’s ANCOVA estimate and interval should be distinguished from the recalculated unadjusted estimate and interval because they arise from different analyses. The record does not give enough model detail to reproduce or evaluate all aspects of the adjusted analysis.

Why is non-inferiority not the same as no difference?

A conventional test for a difference typically evaluates whether the data are inconsistent with a null hypothesis of no difference. A non-inferiority test instead evaluates whether the new treatment is not worse than the comparator by more than a chosen margin. A result can fail to show a conventional difference without establishing non-inferiority. Likewise, a p-value reported for a non-inferiority analysis needs to be interpreted using the stated margin and testing procedure. The margin and the exact decision rule are not reported in the registry record, so the non-inferiority claim cannot be independently checked from the listed estimate, interval, and p-value alone.

The unadjusted recalculation’s p-value is not a replacement for the sponsor’s prespecified non-inferiority test. It addresses a different statistical calculation based on summary statistics. As the record flags a discrepancy, the sponsor’s own analysis takes precedence in describing the reported trial analysis. The recalculation can still help readers understand the posted group summaries, provided its unadjusted status is clear.

What does ANCOVA add?

ANCOVA, or analysis of covariance, compares outcomes between groups while accounting for one or more covariates. In a baseline-and-follow-up setting, an ANCOVA may account for baseline outcome values, but the covariates actually used in this study are not reported in the registry record. Adjustment can produce an estimate that differs from a simple comparison of group-level changes. Differences between adjusted and unadjusted estimates are not necessarily evidence of an error; they may reflect the model, the analysis population, or other analytic choices. The available record does not provide enough detail to determine which choices explain the discrepancy in this trial.

How should the response outcome be understood?

The secondary response outcome is binary: each participant is classified as having or not having a response according to a definition that is not reported in the registry record. A risk difference compares the proportions meeting that classification in the two groups. Its confidence interval reflects uncertainty in that comparison. The registry also lists relative measures for this endpoint, but the definition of response and any prespecified analysis plan are not reported. A binary endpoint therefore cannot be interpreted fully without knowing the response criteria and how missing outcome data were handled.

Why does over-dispersion matter?

Over-dispersion is a general statistical concern for count outcomes when the observed variability is greater than a model expects. It can make standard errors too small if the analysis assumes less variation than the data contain, leading to confidence intervals that are too narrow and p-values that are too small. This is a general concept, not a finding reported for this trial. The primary outcome is a continuous change measure, and the record does not report an over-dispersion analysis. It would not be appropriate to infer that over-dispersion occurred from the listed results.

More generally, estimates and tests depend on assumptions about sampling, measurement, model form, and missingness. The registry record does not report diagnostic checks, sensitivity analyses, or all model specifications. These omissions limit what can be independently assessed, even when numerical estimates and confidence intervals are posted.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate a treatment-group contrast. The recalculated primary mean difference is 0.19 g/L, with a 95% confidence interval from -3.47 to 3.85. The sponsor’s ANCOVA estimate is -0.24 g/L, with a 95% confidence interval from -4.86 to 4.38. The estimates are close to zero in magnitude, but the intervals span values on both sides of zero and permit a range of possible group differences.

The intervals are not interchangeable: one comes from a simple unadjusted recalculation using posted summary statistics, and the other is the sponsor-reported ANCOVA analysis. The record flags a discrepancy, so the sponsor’s analysis takes precedence for the trial’s reported result. The registry does not report enough detail to identify why the two estimates and intervals differ.

For non-inferiority, precision must be judged against the margin rather than by asking only whether the interval includes zero. If the interval extends beyond the unacceptable-loss boundary, the data may not establish non-inferiority; if it is contained within the acceptable region, that may support the criterion, depending on the prespecified method. The non-inferiority margin is not reported in the registry record, so the relationship between either interval and that boundary cannot be assessed.

A confidence interval describes uncertainty in an estimated group effect under the analysis assumptions. It does not show the spread of individual outcomes, which is described by the standard deviation, and it does not guarantee that future results will fall within its limits. The reported standard deviations indicate participant-level variability, while the intervals quantify uncertainty around the group contrast. Both kinds of information matter, but they answer different questions.

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 80% power and participants per arm for 90% power. They are not total event counts. For the continuous primary endpoint, the figures are based on the observed mean difference; for the binary response outcome, the figures are based on the observed response difference. The displayed planning values are illustrations rather than the original design calculation.

The stated 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 set at the stated fraction of the observed effect. The sample-size figures are calculated from the observed effect, not from the trial’s original design assumptions. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation indicates would be needed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding planning number for a 90% chance. These are planning concepts, not guarantees that a future study will obtain a particular result. The calculation does not say how much power this completed trial had for its observed result; this is not observed power.

The rows use planning for 100%, 75%, and 50% of the observed effect. Smaller effects require more participants to detect under the same assumptions. The figures should be read as illustrations of how a target effect size affects planning, not as evidence that the trial was designed for those targets. In particular, they do not establish that the original study was adequately powered for a non-inferiority conclusion, because the original assumptions and non-inferiority margin are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.190; pooled standard deviation σ = 14.806.
2. n = 2 × (1.96 + 0.842)² × 14.806² / 0.190² = 95,327.2, rounded up to 95,328 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.190000000000001                      # observed difference in means
sigma <- 14.8061841404192                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3993288)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 95,328 (80% power), 127,617 (90% power)
 75% of observed effect: n per arm = 169,471 (80% power), 226,873 (90% power)
 50% of observed effect: n per arm = 381,309 (80% power), 510,465 (90% power)
power.t.test: 95328.1 
Simulated power at n = 95,328 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a sponsor ANCOVA analysis of the primary outcome as a non-inferiority analysis. The reported mean difference (net) is -0.24 g/L, with a 95% confidence interval from -4.86 to 4.38 and a p-value of 0.003. This is the analysis to use when describing the sponsor’s reported result.

A separate recalculation from the posted group summaries is unadjusted. It estimates a mean difference of 0.19 g/L, with a 95% confidence interval from -3.47 to 3.85 and an unadjusted p-value of 0.919. The two analyses differ in estimate, interval, and p-value. The record flags this discrepancy, so the sponsor’s own analysis takes precedence over the recalculation.

The recalculation is useful as a transparent descriptive check on the posted means and standard deviations, but it does not recreate the sponsor’s ANCOVA. The covariates, model specification, and analysis details needed to reproduce the ANCOVA are not reported in the registry record. Nor is the non-inferiority margin reported. Therefore, the sponsor’s reported estimate and test can be described, but the precise non-inferiority decision rule cannot be independently verified from the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and several secondary outcomes. When multiple outcomes or multiple statistical tests are examined, the chance of at least one apparently noteworthy result can increase. This is the general multiplicity problem. Common approaches include defining a hierarchy of tests, adjusting significance thresholds, or treating secondary analyses as exploratory. Which approach, if any, was used in this study is not reported in the registry record.

The record gives one sponsor-reported ANCOVA analysis for the primary endpoint and a recalculated unadjusted comparison based on posted summary statistics. It does not report whether additional primary analyses were prespecified, whether interim analyses were planned or performed, or what statistical analysis plan governed the study. Those details are not reported in the registry record and should not be inferred from the posted results.

The primary population definition includes randomized participants who received at least one dose and had hemoglobin measurements before and after treatment. This is the population described for the primary outcome, but it is narrower than a definition that includes every randomized participant regardless of treatment receipt or outcome availability. The record does not describe a separate all-randomized analysis or a per-protocol analysis.

Missing-data procedures are also not reported in the registry record. It is not stated whether missing outcome values were imputed, excluded, handled through a model, or examined in sensitivity analyses. Since the stated primary population requires both pre-treatment and post-treatment hemoglobin data, the way participants without one of those measurements were treated is important to understanding the analysis.

For non-inferiority, analysis-population choices and missing-data handling are especially relevant because different assumptions can influence whether a treatment difference appears to remain within an acceptable margin. The registry does not report the margin, its justification, or the planned sensitivity analyses. As a result, the record allows readers to identify the reported endpoint and analysis but does not provide the full framework needed to evaluate multiplicity, robustness, or the non-inferiority decision.

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: menometrorrhagia (0.8%), encephalopathy (0.8%).

The registry reports serious adverse events among participants at risk: 2 for Ferrum Lek and 0 for MALTOFER. It also reports 54 participants with other adverse events for Ferrum Lek and 47 for MALTOFER. One death is listed in the Ferrum Lek group and 0 in the MALTOFER group. These are descriptive counts in the registry record; they do not by themselves establish that a treatment caused an event or that a difference between groups is reliable.

The serious-event terms listed are Menometrorrhagia and Encephalopathy, each shown as 0.8%. The record does not provide event narratives, timing, severity details beyond the serious-event classification, or a causal assessment for these terms. It also does not provide a statistical comparison or confidence interval for the safety counts.

Safety counts should be interpreted in light of the number of participants at risk, the duration of observation, and how events were collected and classified. The record lists 133 participants at risk for serious and other adverse events in the Ferrum Lek group and 134 in the MALTOFER group. Treatment exposure was described as 12 weeks. Further details about event surveillance and follow-up are not reported in the registry record.

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

The posted data describe a randomized comparison of Ferrum Lek and MALTOFER for mild and moderate iron-deficiency anaemia, with change in hemoglobin from baseline to Week 12 as the primary endpoint. The registry reports both group summaries and a sponsor ANCOVA analysis labeled as non-inferiority. The recalculated unadjusted comparison differs from the sponsor analysis, and the record flags that discrepancy; the sponsor’s own analysis takes precedence.

The sponsor’s estimate and confidence interval describe the reported adjusted comparison, but the non-inferiority margin is not reported in the registry record. Without that boundary and the decision rule, the posted p-value cannot by itself establish whether the trial met its non-inferiority objective. The confidence interval also includes values on both sides of zero, and its relevance to non-inferiority depends on the missing margin and the direction defined by the protocol.

The results do not establish that the two treatments are identical. A non-significant unadjusted comparison is not proof of equivalence, and equivalence would require its own prespecified framework and margins. Conversely, the sponsor’s reported non-inferiority analysis should not be dismissed because a separate unadjusted recalculation has a different p-value. The analyses answer different statistical formulations, and the registry record does not contain all the information needed to reconcile them.

The endpoint is a group-level change measure. It does not, on its own, convey every participant’s course, the distribution of individual responses, or the complete balance of benefits and harms. The safety counts are descriptive, and the secondary outcomes provide additional but incomplete context. A full interpretation would require the protocol or statistical analysis plan, including the non-inferiority margin, analysis populations, missing-data procedures, multiplicity approach, and details of the sponsor’s ANCOVA.

Accordingly, the defensible reading is limited to what the registry reports: the endpoint, group summaries, sponsor analysis, secondary response comparison, and adverse-event counts. The record does not support broader claims about exact equivalence, clinical importance, or the robustness of the non-inferiority conclusion.

18. Why This Trial Matters Statistically

This study illustrates why a non-inferiority result cannot be interpreted from a p-value alone. The central question is whether the plausible treatment differences are contained within a prespecified acceptable boundary. Without the margin, even a sponsor-reported analysis labeled non-inferiority cannot be fully checked against the criterion that gives the test its meaning.

It also illustrates the distinction between an adjusted analysis and a simple recalculation from summary statistics. The posted group means and standard deviations permit an unadjusted comparison, while the sponsor reports an ANCOVA estimate. These methods need not return identical estimates. When the record flags a discrepancy, the sponsor’s own analysis takes precedence, but readers still benefit from knowing that a separate unadjusted calculation does not reproduce it. Complete model details would make the relationship more transparent.

The trial also shows why an analysis population needs careful reading. The primary population is defined by treatment receipt and availability of hemoglobin measurements before and after treatment. That definition is relevant to missing-data concerns and to the interpretation of a non-inferiority comparison. The record does not provide the complementary analyses needed to assess how sensitive the result is to those choices.

Finally, a collection of secondary endpoints and safety counts can broaden the descriptive picture without resolving the primary statistical question. Multiplicity, outcome definitions, follow-up, and missingness all affect how much weight those additional results can bear. Clear reporting of these elements is essential for researchers assessing precision and reproducibility, not just the direction of the estimates.

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 details needed to assess the primary non-inferiority claim are not reported in the registry record. Most importantly, the non-inferiority margin and its justification are absent. The record also does not give the decision rule or enough detail about the sponsor’s ANCOVA to reproduce the adjusted analysis. The discrepancy between the sponsor result and the unadjusted recalculation therefore cannot be resolved from the posted information.

The stated primary analysis population requires participants to have received at least one dose and to have hemoglobin data before and after treatment. The record does not describe outcomes for randomized participants who did not meet that definition, a separate per-protocol analysis, or sensitivity analyses for missing measurements. This is a particular concern for interpreting non-inferiority, where analysis choices can affect the conclusion.

The study was open-label, and masking of laboratory staff or outcome assessors is not reported. The record does not provide details of the randomization process, allocation concealment, adherence, protocol deviations, or the handling of measurements outside the intended visit window. These are not evidence of a flaw, but they limit what can be evaluated from the registry record.

Five secondary outcomes are listed, but numerical results are not reported for all of them in the information available. The response outcome definition is not reported, and multiplicity procedures are not described. Safety results are presented as counts without comparative uncertainty estimates or detailed event narratives. The record also does not report whether interim analyses occurred or provide the original design assumptions and sample-size justification.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Test the Hypothesis of Non-inferior Efficacy and Safety of Ferrum Lek® (Iron (III) Hydroxide Polymaltosate), 100 mg Chewable Tablets (Lek d.d., Slovenia), as Compared With MALTOFER® (Vifor S.A., Switzerland), in Subjects With Mild and Moderate Iron Deficiency Anemia. — NCT03993288.
• Registry record last updated 2021-07-12; status last verified 2021-06.
• Results first posted 2021-07-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, open-label, parallel-group phase 3 study comparing Ferrum Lek with MALTOFER in patients with mild and moderate iron-deficiency anaemia. Both groups received 2 tablets daily (200 mg) for 12 weeks. Enrollment was 267.

The primary endpoint was change in blood hemoglobin level from baseline to Week 12. The sponsor reported an ANCOVA non-inferiority analysis, while a separate unadjusted recalculation from the posted summary statistics differs; the record flags the discrepancy, so the sponsor’s own analysis takes precedence. The non-inferiority margin is not reported in the registry record, limiting independent interpretation of the claim.

The record lists secondary laboratory outcomes, a response outcome, and adverse-event counts. Secondary-result completeness, missing-data methods, multiplicity procedures, and further analysis details are not reported in the registry record.