Clinical Evaluation of Iron Treatment Efficiency Among Non-anemic But Iron-deficient Female Blood Donors: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Evaluation of Iron Treatment Efficiency Among Non-anemic But Iron-deficient Female Blood Donors (NCT00689793), a randomized phase 4 study. The primary outcome is Level of Fatigue Before and After Iron Treatment/Placebo, Using a 10 Point Visual Analogue Scale..

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, phase 4 trial sponsored by the University of Lausanne. The registry record marks the study as completed. Its listed start is 2008-11, and its primary completion is 2010-10. The record gives enrollment as 154. It describes quadruple masking but does not specify in the information available for this summary which roles the masking covered or how it was implemented.

The two arms were oral treatment of iron and placebo. The intervention is listed as ferrous sulphate; the brief summary names Tardyferon® as the iron substitution. Arm descriptions are blank in the registry record. Dose, treatment schedule, and further details about the placebo are not reported in the registry record. The primary outcome was assessed at baseline and after 4 weeks.

The trial population was female blood donors described as non-anemic and iron-deficient, with the brief summary referring to mean serum ferritin < 30ng/ml. Fatigue and iron deficiency are the listed conditions. The record also lists outcomes concerning hemoglobin, ferritin, aerobic capacity, mental disorder, and treatment adherence. It does not give further details about the eligibility criteria, recruitment setting, or the analysis population in the information summarized for the trial.

The posted primary arm summaries include 74 for oral iron and 71 for placebo. These are the arm counts accompanying the posted outcome summaries; they should not be treated as a reconciliation of the enrollment figure. The registry record does not report why the outcome counts differ from the enrollment figure or whether all randomized volunteers contributed to every analysis.

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: One week after whole blood donation, participants were randomized if they were not anemic and their ferritin level was \< or = 30 ng/mL.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The sample size for randomized volunteers was calculated using a two-sample comparison of means to detect a one point difference in the visual analogical scale (first outcome).

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 Level of Fatigue Before and After Iron Treatment/Placebo, Using a 10 Point Visual Analogue Scale., measured over baseline and 4 weeks.

The primary endpoint measures perceived fatigue using a 10-point visual analogue scale. The anchors are no fatigue=0 and very severe fatigue=10. Scores were collected at baseline and after 4 weeks of iron treatment or placebo. The outcome is continuous: it represents a measured scale value, and the posted arm summaries describe means and standard deviations.

A fatigue rating is relevant to the trial’s stated question because the study aimed to assess the subjective response to iron substitution in female blood donors. It captures participants’ reported experience rather than a laboratory measurement. The scale provides a numerical way to compare average fatigue between the randomized groups and to describe change over the stated follow-up period.

The registry record names the endpoint as the level of fatigue before and after treatment or placebo. It does not report details about how participants completed the scale, whether the same procedures were used at both assessments, or how missing ratings were handled. The trial’s stated design rationale refers to detecting a one point difference, but the registry record does not report the full assumptions behind that calculation.

Interpretation should retain the scale’s direction and anchors: higher values indicate more severe fatigue. An average difference describes a group-level contrast and does not indicate that every participant experienced a similar change. The posted summary statistics alone do not show the distribution of individual responses.

7. Results Posted in the Registry

• Oral Treatment of Iron: mean 3.40 versus 3.50 on control; difference -0.10 (95% CI -0.90 to 0.70), standardized effect d = -0.04; z-test p = 0.806.

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.

Hemoglobin Variation Before and After Treatment vs Placebo

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Oral Treatment of Iron: mean 135.00 versus 130.00 on control; difference 5.00 (95% CI 3.04 to 6.96), standardized effect d = 0.83; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Oral Treatment of Iron than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Ferritin Change Before and After 4 Weeks of Treatment/Placebo

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Oral Treatment of Iron: mean 28.00 versus 12.90 on control; difference 15.10 (95% CI 12.15 to 18.05), standardized effect d = 1.66; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Oral Treatment of Iron than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Aerobic Capacity Using an Indirect Measurement of VO2Max : Chester Step Test

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Oral Treatment of Iron: mean 40.50 versus 40.10 on control; difference 0.40 (95% CI -4.75 to 5.55), standardized effect d = 0.03; z-test p = 0.879.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oral Treatment of Iron and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome pattern is mixed. The posted results show between-arm contrasts for the blood measures, while the aerobic-capacity comparison is close to zero and imprecise. These outcomes address different aspects of the study: laboratory measures, physical capacity, and other listed domains do not measure the same thing as perceived fatigue. Their pattern does not replace or negate the primary fatigue result.

Secondary outcomes may help describe what changed during the study, but their evidential weight depends on how they were planned and analyzed. The registry record lists outcomes concerning hemoglobin, ferritin, aerobic capacity, mental disorder, and adherence, while the posted analysis details do not cover every listed outcome. The record does not report a prespecified hierarchy, adjustment for multiple testing, or how unreported analyses were selected. Without those details, nominally significant secondary findings should be interpreted cautiously.

Multiplicity matters because testing several outcomes increases the chance that at least one result will appear statistically persuasive even when no corresponding effect exists. This is a general statistical concern, not evidence that any particular secondary result is false. Unadjusted secondary p-values do not carry the same confirmatory weight as a prespecified primary analysis, especially when the analysis plan and missing results are unclear.

The secondary results can be viewed as context for the trial’s overall pattern, but they do not establish a fatigue benefit. They also do not resolve uncertainty in the primary endpoint. The registry record does not report enough about the secondary analysis plan to determine which results were intended as confirmatory and which were exploratory.

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

• Hemoglobin Variation Before and After Treatment vs Placebo
• Ferritin Change Before and After 4 Weeks of Treatment/Placebo
• Aerobic Capacity Using an Indirect Measurement of VO2Max : Chester Step Test
• Response of Iron Supplementation on Mental Disorder
• Adherence to Treatment.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, so the posted summaries use a mean and standard deviation for each arm. A mean describes the group’s average score. A standard deviation describes how dispersed individual scores are around that average; it is not the uncertainty interval for the mean. The primary scale runs from no fatigue=0 to very severe fatigue=10, so a lower average corresponds to less reported fatigue on that scale.

What does a mean difference represent?

The simple unadjusted recalculation subtracts the placebo mean from the oral-iron mean. The resulting estimate is -0.1 points. A negative value means the observed average was lower in the oral-iron arm; it does not by itself establish that the treatment caused the difference. Randomization supports a between-group comparison, but uncertainty remains, and the registry record does not report adjustment details for this recalculation.

The recalculated comparison uses the posted arm means, standard deviations, and counts. It is an unadjusted comparison, not the sponsor’s reported regression. The recalculated p-value is 0.806. A p-value describes how compatible the observed result is with a specified null model; it is not the probability that the null hypothesis is true, nor the probability that the result occurred by chance. A large p-value does not establish no effect or equivalence.

What does a confidence interval add?

A confidence interval communicates uncertainty around an estimate. In general, a 95% confidence interval is generated by a method that, under its assumptions and repeated use, would cover the target parameter in 95% of such intervals. It gives a range of values compatible with the data and method; it is not a guarantee that the particular interval contains the true value. The recalculated primary interval crosses zero, leaving both negative and positive mean differences compatible with the summary data at that confidence level.

The sponsor reports a linear regression analysis of final values, with a mean difference of 1, a 95% confidence interval from 0 to 10, and p=0.69. A regression result can differ from a simple unadjusted contrast if the analysis uses additional model terms or a different specification. The registry record does not report the covariates or full model details, so it is not possible to identify the reason for the difference. Because the record does not flag a discrepancy, both results can be described, but the sponsor’s own analysis is the trial’s reported analysis.

Why can the estimate and the p-value be inconclusive?

Precision depends on the size of the estimated effect and the variability and amount of information in the data. When scores vary considerably around group means, a small estimated difference may be difficult to distinguish from sampling uncertainty. A confidence interval crossing zero means the data do not rule out no mean difference under that method; it does not show that the true difference is exactly zero. General statistical interpretation also depends on the assumptions of the comparison, including appropriate measurement and analysis of participants’ outcomes.

Over-dispersion is a general concern when outcome variability is larger than a statistical model expects. If a model underestimates variability, standard errors can be too small and intervals too narrow. The primary outcome is analyzed as a continuous measure with standard deviations, and the registry record does not report a model diagnosing over-dispersion. It therefore should not be asserted that over-dispersion occurred in this trial. More generally, checking whether a model’s variability assumptions fit the data is part of sound analysis.

What is the distinction between the reported and recalculated analyses?

The recalculation is based only on group-level summaries and is unadjusted. It does not reproduce a regression using participant-level data, account for any covariates, or address missing outcomes. The sponsor’s reported analysis is identified as linear regression and concerns final values. The registry record does not report enough model detail to reconstruct that analysis. The reported and recalculated results therefore answer closely related but not necessarily identical statistical questions.

The registry record states that the randomized sample size was calculated using a two-sample comparison of means to detect a one point difference in the visual analogue scale. The original design’s significance level, target power, allocation assumptions, variability assumptions, and any allowance for missing data are not reported in the registry record. Those omissions limit independent assessment of the original design calculation. The separate planning illustrations use stated assumptions and the observed effect; they are not evidence of the trial’s original plan or of the probability that the completed trial detected an effect.

How should secondary analyses be treated?

Secondary outcomes can broaden the scientific picture, but each additional test creates more opportunity for a chance finding. Unless a plan controls the overall error rate or distinguishes confirmatory from exploratory outcomes, isolated unadjusted p-values carry less weight. The registry record does not report multiplicity adjustment or a hierarchy for secondary outcomes. General statistical practice is to interpret those analyses with their uncertainty and relationship to the primary question, rather than treating every nominally significant result as independently conclusive.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data and analysis constrain an estimated effect. The recalculated primary mean difference is -0.1 points, but its confidence interval crosses zero and includes values on both sides of no difference. This means the estimate is not precise enough to establish the direction of the underlying mean contrast. The interval should be considered alongside the observed variability in fatigue scores, rather than reading the point estimate alone.

The sponsor’s reported primary result is a mean difference of 1, with a 95% confidence interval from 0 to 10 and p=0.69. This is the result of the registry’s reported regression analysis, not the same calculation as the unadjusted estimate from group summaries. The registry record does not give the regression specification or explain the relationship between the two summaries. The sponsor’s own analysis takes precedence as the reported trial analysis, while the recalculation remains a separate descriptive check.

In general, a confidence interval represents the range of parameter values reasonably compatible with the data and the method, subject to its assumptions. Wider intervals indicate less precision; narrow intervals indicate more precision, but neither alone determines whether an effect matters clinically. The registry record does not report a threshold for a clinically important difference in fatigue. Therefore, these results cannot be classified against such a threshold from the registry information.

The confidence interval crossing zero should not be described as proof of no effect. Nor does a non-significant p-value establish equivalence. A study designed for equivalence would require an explicit margin and a corresponding analysis; neither is reported in the registry record. The interval and p-value instead communicate uncertainty in the tested comparison.

12. Planning a Similar Trial: Sample Size

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

The sample-size table and curve are planning illustrations based on the observed effect, not the trial’s original design calculation. The figures are participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning scenarios use the stated fraction of the observed effect. For the continuous outcomes, the figures refer to participants per arm.

The 80% power column describes the planned number of participants per arm under which a hypothetical study would have an 80% chance of detecting the assumed effect at the stated significance level, if the planning model and assumptions hold. The 90% column represents a higher chance of detecting that assumed effect and therefore generally requires more participants per arm. These are design concepts, not guarantees about a particular trial.

Rows planning for 75% or 50% of the observed effect assume a smaller difference than the full observed effect. Smaller effects are harder to distinguish from random variation, so those scenarios require more participants per arm. The illustrated figures can change substantially because the observed effect is used as the starting point, and observed estimates can be unstable. The figures are not observed power and do not describe the probability that this completed trial detected an effect.

The registry record states that the trial’s randomized sample size was calculated using a two-sample comparison of means to detect a one point difference on the fatigue scale. Its original significance level, target power, and other calculation assumptions are not reported in the registry record. The planning illustrations should therefore be kept separate from the stated original design rationale.

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 = -0.100; pooled standard deviation σ = 2.449.
2. n = 2 × (1.96 + 0.842)² × 2.449² / -0.100² = 9,418.4, rounded up to 9,419 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 <- -0.1                      # observed difference in means
sigma <- 2.44946119378531                     # 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(689793)
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 = 9,419 (80% power), 12,609 (90% power)
 75% of observed effect: n per arm = 16,744 (80% power), 22,416 (90% power)
 50% of observed effect: n per arm = 37,674 (80% power), 50,435 (90% power)
power.t.test: 9419.4 
Simulated power at n = 9,419 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 record reports a sponsor analysis for fatigue using linear regression of final values. It gives a mean difference of 1, a 95% confidence interval from 0 to 10, and p=0.69. The unadjusted recalculation from the posted group summaries gives a mean difference of -0.1 and p=0.806; its interval crosses zero. These figures are not identical, and the registry record does not provide the regression specification or participant-level details needed to reproduce the sponsor’s result.

The recalculation is a simple comparison of posted means and standard deviations. It is not a replacement for a regression analysis and does not account for any adjustment the sponsor may have made. The registry record does not describe such adjustment, so its role cannot be inferred. The trial’s reported analysis is the sponsor’s analysis, which takes precedence for describing what the sponsor concluded. The recalculation is useful as a transparent, unadjusted check based on the posted summaries, but it should not be presented as the trial’s official model result.

The registry record does not flag a discrepancy. That does not explain the difference between the results or establish that they estimate precisely the same quantity. A careful reading keeps the sponsor analysis and the recalculation distinct and notes that both leave substantial uncertainty about the primary fatigue comparison.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary endpoint and several secondary outcomes, but it does not report how multiplicity was handled. When several outcomes are tested, the chance of at least one apparently positive result can increase. A prespecified hierarchy, adjustment procedure, or clear distinction between confirmatory and exploratory analyses can help address that issue. None is reported in the registry record, so secondary p-values should be read as unadjusted unless otherwise specified.

The record does not report a missing-data method for the primary or secondary outcomes. It does not state whether missing measurements were excluded, imputed, or handled through a model, nor does it describe reasons for missingness. The posted outcome counts should not be assumed to represent all randomized volunteers or a particular analysis population. The registry record does not report whether the analyses followed intention-to-treat, per-protocol, or another population definition.

Further details about the statistical analysis plan are also not reported in the registry record. This includes any planned covariate adjustment, sensitivity analyses, interim analyses, and procedures for selecting among analyses. The sponsor’s primary analysis is identified as linear regression of final values, but model terms and assumptions are not described in the information.

These omissions limit assessment of whether the reported analyses followed a prespecified plan and how robust they are to missing outcomes or alternative assumptions. They do not prove that the analyses were inappropriate; they mean the registry record does not provide the information needed to evaluate those questions. The stated original sample-size rationale is a two-sample comparison of means intended to detect a one point difference, but the original calculation’s other assumptions are not reported.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event summaries report 0 affected participants in the oral-iron arm and 0 in the placebo arm. The listed counts at risk are 74 for oral iron and 71 for placebo. No serious adverse event terms are listed. These figures describe what is recorded in the registry summary; they should not be interpreted as proof that serious harms cannot occur.

The other adverse event summaries list 29 affected participants for oral iron and 11 for placebo. These are not the serious adverse event counts and should not be conflated with them. The registry record does not provide event descriptions in the information, and it does not report deaths as a numeric count. A blank death count is not evidence that there were no deaths; that information is not reported in the registry record.

Safety comparisons depend on definitions, follow-up, ascertainment, and completeness of reporting. The registry record does not provide enough detail to assess those features or to infer a causal relationship from the counts. These summaries are descriptive and do not establish the full safety profile of either treatment.

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

The primary fatigue results show similar posted group means after 4 weeks, with a small unadjusted difference and substantial uncertainty. The recalculated comparison does not establish a difference in average fatigue, but it also does not prove that the treatments are equivalent or that there is no effect. The sponsor’s reported regression likewise has p=0.69 and a confidence interval from 0 to 10; the registry record does not report enough model detail to reconcile it with the recalculation.

The result applies to the trial population and the recorded assessment period: non-anemic, iron-deficient female blood donors, assessed at baseline and after 4 weeks. It should not be generalized automatically to other populations, other treatment schedules, or longer follow-up. Additional eligibility and treatment details are not reported in the registry record.

The secondary blood-measure findings do not answer the primary question about perceived fatigue. A change in a laboratory measure is a different outcome from a participant’s fatigue score. Similarly, the posted aerobic-capacity comparison does not determine whether participants felt less fatigued. These outcomes can provide context, but they cannot substitute for the primary endpoint.

The registry record does not report a clinically important difference threshold for fatigue. Statistical uncertainty therefore cannot be translated into a judgment about clinical importance using the information in the record. Nor can the posted results establish the effect for every individual participant: group means do not describe each person’s response.

In short, the record documents a randomized comparison and reports both sponsor and unadjusted summaries. The primary endpoint does not provide clear evidence of a between-group fatigue difference, while the uncertainty and reporting limitations leave open a range of possible effects. This is a description of the posted data, not medical advice.

18. Why This Trial Matters Statistically

This trial illustrates why a primary patient-reported outcome should be interpreted separately from laboratory outcomes. The study’s central question concerns perceived fatigue, while its secondary outcomes include measures such as hemoglobin and ferritin. Statistical evidence for a difference in one type of measure does not automatically answer a question about another.

It also illustrates the value of distinguishing a sponsor-reported model from a recalculation based on group summaries. The sponsor reports linear regression of final values; the recalculation is an unadjusted comparison. Their estimates and p-values differ, and the registry record does not give enough detail to determine why. Keeping those analyses distinct makes the limits of summary-level recalculation clear rather than implying it reproduces the original model.

Precision matters alongside statistical significance. The primary estimate is small, and its uncertainty crosses no difference. A non-significant result is not proof of equivalence, just as a statistically notable secondary finding is not automatically confirmatory. Interpretation depends on the planned question, model, uncertainty, and reporting context.

Finally, planning illustrations based on observed effects are not the original design calculation and do not describe observed power. Separating these quantities helps avoid treating a post hoc planning scenario as evidence about whether the completed study was adequately powered. The registry record supplies a limited original design rationale but does not report its full assumptions.

19. Limitations

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

The registry record leaves important details about trial conduct and analysis unreported. It does not describe the precise eligibility thresholds beyond the brief characterization of the population, the treatment dose, or how the placebo was matched. It also does not explain which roles were masked or how masking was maintained. These gaps limit assessment of how closely the recorded design details can be evaluated.

The outcome counts do not match the enrollment figure, and the registry record does not explain the difference. It does not report participant flow, reasons for missing outcome data, or the analysis population. Thus the posted counts cannot establish whether all randomized volunteers were included or how incomplete observations affected the results.

The sponsor’s primary regression is reported without its model specification. The registry record does not explain why its reported estimate differs from the simple unadjusted recalculation, and the information available is not sufficient to reproduce the regression. This restricts interpretation of the relation between the reported model and the posted arm summaries.

The record also does not report multiplicity procedures, a hierarchy for secondary outcomes, a clinically important fatigue threshold, or a complete statistical analysis plan. It lists more outcomes than the posted analyses cover, without explaining the distinction. Consequently, secondary findings warrant caution, and the robustness of the primary result to missing-data and model choices cannot be assessed from this record alone.

These are limitations of the information reported in the registry record; they do not establish that trial procedures were inadequate. They identify what cannot be judged from the posted information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Evaluation of Iron Treatment Efficiency Among Non-anemic But Iron-deficient Female Blood Donors — NCT00689793.
• Registry record last updated 2013-02-15; status last verified 2013-01.
• Results first posted 2013-02-15.
• 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

NCT00689793 is a completed, randomized, quadruple-masked, parallel-group phase 4 trial sponsored by the University of Lausanne. It enrolled female blood donors described as non-anemic and iron-deficient and compared oral iron treatment with placebo. The primary outcome was fatigue on a 10-point visual analogue scale at baseline and after 4 weeks.

The posted primary summaries show means of 3.4 for oral iron and 3.5 for placebo. The unadjusted recalculation estimates a mean difference of -0.1, with p=0.806; its confidence interval crosses zero. The sponsor’s reported linear regression gives a mean difference of 1, a 95% confidence interval from 0 to 10, and p=0.69. The registry record does not provide enough detail to reconcile the analyses.

The record also reports secondary measures, but does not report multiplicity handling, missing-data methods, or the full statistical plan. The primary fatigue result is uncertain and does not establish either a difference or equivalence.