Safety and Tolerability of Intravenous VIT-45 in Patients With Iron Deficiency Anemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Tolerability of Intravenous VIT-45 in Patients With Iron Deficiency Anemia (NCT00740246), a randomized phase 3 study. The primary outcome is Incidence of Treatment-emergent Adverse Events During Each 7-day Study Period.

2. Clinical Question

3. Trial Design

The registry identifies this as a Phase 3, randomized, double-blind, placebo-controlled, multicenter crossover study. Participants were assigned to one of two treatment sequences: VIT-45 on Day 0 followed by placebo on Day 7, or placebo on Day 0 followed by VIT-45 on Day 7. Thus, the sequence descriptions indicate that both treatments were scheduled for each participant, at different times. The registry reports total enrollment of 594 and a completed study.

For the VIT-45 administration, the described dose was 15 mg/kg, up to a maximum dose of 1,000 mg of iron, given intravenously over 15 minutes. Placebo was described as normal saline, with volume depending on weight: 250 cc for weight greater than 33 kg and 100 cc for weight at or below 33 kg, also infused over 15 minutes. The registry gives the study start as 2005-07 and primary completion as 2006-02.

The primary outcome is described as the number of participants with any treatment-emergent adverse event during each 7-day study period. For Study Period 1, the period ended when dosing for Study Period 2 began; for Study Period 2, it ended with completion of Day 14 procedures. These timing details matter because the registry summarizes event counts by treatment exposure across the two periods. The posted counts are 584 participants for VIT-45 and 569 for placebo; these are treatment-specific outcome denominators, not the overall enrollment figure. The registry record does not explain why those denominators differ from total enrollment or provide additional details about participant flow.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: At Least 1 Treatment-Emergent Adverse Event

5. Baseline Characteristics

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

Population: Safety population: All subjects who received at least 1 dose of randomized study drug

6. Primary Endpoint

The registry lists the primary outcome as Incidence of Treatment-emergent Adverse Events During Each 7-day Study Period, measured over Day 0 to 7.

The primary endpoint counts participants who experienced at least one treatment-emergent adverse event during a 7-day study period. It is a binary participant-level outcome: a participant either had one or more such events during the period or did not. The reported counts therefore refer to participants, not to the total number of separate event episodes. A participant with multiple events still contributes once to this endpoint for that treatment period.

The registry defines Study Period 1 as ending when dosing for Study Period 2 began, and Study Period 2 as ending with completion of Day 14 procedures. The outcome is reported for VIT-45 exposure and placebo exposure. It is used to describe the incidence of events following each treatment in the periods specified by the study record. It does not, by itself, indicate whether an event was serious, how long it lasted, or whether it was caused by treatment. Serious and other adverse-event counts are separately reported in the safety information.

Because the study used a crossover sequence, the endpoint’s interpretation depends on period and treatment exposure. The record does not report a separate outcome analysis by sequence or period, nor does it describe a statistical method that accounts for within-participant pairing. Those details would be relevant to understanding how the crossover structure was handled in an inferential analysis.

7. Results Posted in the Registry

• ViT-45: 29.8% (174/584) versus 20.0% (114/569) on control; risk difference 9.8 percentage points (95% CI 4.8 to 14.7), risk ratio 1.49 (1.21–1.83); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry presents a binary endpoint: whether a participant experienced at least one treatment-emergent adverse event during a study period. For this type of outcome, a proportion is the number of participants with the event divided by the number assessed for that treatment. The posted proportions are 0.298 for VIT-45 and 0.200 for placebo. The event counts and denominators are reported as 174 of 584 and 114 of 569, respectively.

What does the risk difference express?

The risk difference subtracts the comparator event proportion from the intervention event proportion. In this record, the estimate is 0.098, with VIT-45 as the first treatment in the comparison and placebo as the comparator. A positive estimate means that the observed event proportion was higher in the VIT-45 exposure group in this unadjusted comparison. The measure is on an absolute scale: it describes the separation between proportions, rather than a relative multiplier.

Other statistical measures can express the same comparison differently. A risk ratio compares proportions by division, while an odds ratio compares event odds. The registry lists relative estimates as well, but the primary interpretation focuses on the risk difference because it directly expresses the absolute contrast in the posted proportions. Different measures answer related but nonidentical questions and should not be treated as interchangeable.

What does the p-value tell a reader?

The posted p-value is <0.001 for the unadjusted comparison. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model, assuming that model and its assumptions apply. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A small p-value does not resolve limitations in the design, measurement, or statistical model.

The record labels the comparison unadjusted. No adjustment for the crossover structure, baseline characteristics, or other factors is described in the registry record. In a crossover study, a participant may contribute observations under both treatments. Those observations can be correlated because they come from the same person. General statistical practice distinguishes a paired analysis, which models within-person comparisons, from an analysis that treats treatment groups as independent. The registry record does not state which approach was used for a formal sponsor analysis, and no analysis entries are listed. Therefore, the posted comparison can be described, but its handling of pairing cannot be established from the record.

Why can over-dispersion matter?

General explanation: for count outcomes, a simple model may assume that variation follows a particular relationship to the mean. Over-dispersion occurs when the observed variation is greater than that assumption allows. It can make standard errors too small if ignored, which can make confidence intervals too narrow and p-values too small. This concern is most relevant when the outcome is a count of events, rather than a binary indicator of whether a participant had at least one event. The primary outcome is reported as participants with an event, so the endpoint itself is binary; the registry does not report an event-count model or an over-dispersion assessment.

General explanation: confidence intervals quantify uncertainty around an estimate under the method used to calculate them. For a risk difference, a confidence interval that includes zero is compatible with no absolute difference under the chosen method; an interval wholly above or below zero is not compatible with zero at the corresponding confidence level, subject to the method’s assumptions. The posted interval runs from 0.048 to 0.147 and does not include zero. This describes statistical precision for the reported unadjusted estimate, not certainty about causation or the applicability of the finding beyond the study population and periods.

What aspects of the analysis are not described?

The registry record does not report the original statistical analysis plan, the method used for the crossover comparison, an approach for missing outcome data, or a definition of the analysis population beyond the posted outcome description. It also does not report interim analyses or a sample-size justification. These omissions prevent a complete reconstruction of the planned inferential methods. General statistical explanations can clarify what the posted measures mean, but cannot substitute for those unreported trial-specific details.

10. Confidence Intervals and Precision

The estimated risk difference is 0.098, with a 95% confidence interval from 0.048 to 0.147. The interval represents uncertainty around the estimated absolute difference under the unadjusted calculation. Its lower and upper limits are both above zero, so the range of values compatible with this calculation does not include no difference. The interval’s width also shows that the estimate is not known exactly; the data support a range of possible contrasts rather than a single certain value.

Precision is not the same as clinical importance. A confidence interval describes statistical uncertainty, while judging the importance of an event difference requires context about the nature, severity, duration, and consequences of events. The registry reports the primary outcome as any treatment-emergent adverse event and separately gives some safety counts, but it does not provide enough detail in this outcome to characterize the full clinical meaning of each event.

The interval is for the unadjusted risk difference reported from treatment-specific counts. Because the study was a crossover, within-participant dependence and period effects may matter for inference. The registry record does not explain whether the interval calculation accounted for those features. Its precision should therefore be understood as precision for the posted comparison, not as confirmation that all relevant design features were modeled.

The reported p-value, <0.001, addresses compatibility with a null comparison under the unadjusted analysis assumptions. It is not a measure of precision and does not replace the confidence interval. Neither statistic establishes causality, describes outcomes outside the 7-day periods, or resolves the unreported details of the analysis population and missing-data handling.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the two-arm comparison, not total events. They are illustrations based on the observed effect, rather than the trial’s original design justification. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The registry record does not report the trial’s original sample-size assumptions or justification.

The 80% power column gives the planned number of participants per arm for a design with an 80% chance of detecting the specified effect if that effect is the true one and the planning assumptions hold. The 90% power column gives the corresponding per-arm number for a 90% chance. These are design calculations, not descriptions of what happened in the trial.

Planning for 100% of the observed effect gives 308 participants per arm for 80% power and 411 participants per arm for 90% power. Planning for 75% of the observed effect gives 529 participants per arm for 80% power and 708 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,148 participants per arm for 80% power and 1,536 participants per arm for 90% power. The pattern illustrates a general principle: smaller effects are harder to detect and require more participants under otherwise unchanged assumptions. These figures are planning illustrations, not observed power.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.200; treatment proportion p₁ = 0.298; average p̄ = 0.249.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6117 = 1.1989.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6078 = 0.5115.
4. n = (1.1989 + 0.5115)² / (0.0976)² = 307.1, rounded up to 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 <- 0.200351493848858                          # control proportion
p1 <- 0.297945205479452                          # 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(740246)
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 = 308 (80% power), 411 (90% power)
 75% of observed effect: n per arm = 529 (80% power), 708 (90% power)
 50% of observed effect: n per arm = 1,148 (80% power), 1,536 (90% power)
power.prop.test: 307.1 
Simulated power at n = 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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and no posted secondary outcome measures. It also lists zero analysis entries. These registry entries limit what can be established about how many formal comparisons were planned or reported, and whether any multiplicity strategy was used. A multiplicity adjustment, such as a prespecified approach to controlling false-positive risk across several tests, is not reported in the registry record. With only the posted primary outcome available, the record does not establish whether other planned endpoints or exploratory analyses existed.

The registry record does not report how missing outcome data were handled, whether participants with incomplete periods were excluded, or what analysis population was used for the posted comparison. It does not describe imputation, sensitivity analyses, or a rule for assigning outcome status when a participant’s event information was incomplete. The different treatment-specific denominators are visible in the posted outcome, but the reason for that difference is not reported in the registry record. No explanation should be inferred from the counts alone.

The crossover design also raises analysis questions that the record does not answer. It does not report whether the analysis accounted for the fact that participants were scheduled to receive both treatments, whether period and sequence were modeled, or how potential carryover between periods was addressed. The posted unadjusted risk difference and p-value describe the reported comparison; they do not establish that a paired crossover analysis was used.

These are reporting limitations, not evidence that a particular method was or was not used outside the information in the registry. Without an analysis plan or fuller results report in the registry record, readers cannot verify the prespecified multiplicity approach, the handling of missingness, or the analysis population.

14. 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: diabetes mellitus non-insulin dependent (0.2%), hypertension (0.2%), upper gastrointestinal hemorrhage (0.2%), pneumothorax (0.2%), endometritis (0.2%).

The safety summary reports participants with serious adverse events, other adverse events, and deaths across exposure groups labeled “VIT-45 on Day 0 or Day 7” and “Placebo on Day 0 or Day 7.” For VIT-45 exposure, 2 participants were reported with serious adverse events, 31 with other adverse events, and 1 death; the group at risk was 584. For placebo exposure, 4 participants were reported with serious adverse events, 19 with other adverse events, and 0 deaths; the group at risk was 569.

These are counts for the exposure groups as described, not a participant-by-participant account of timing, cause, or event overlap. The record does not state whether a participant could appear in more than one event category or give enough information to attribute a death to treatment. It also lists serious-event terms with reported frequencies of 0.2% each, including diabetes mellitus non-insulin dependent, hypertension, upper gastrointestinal hemorrhage, pneumothorax, endometritis, and fall. These figures should be read as registry safety summaries, not as proof that treatment caused or prevented any particular event.

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

The posted results show that treatment-emergent adverse events were recorded for 174 of 584 participants during VIT-45 exposure and 114 of 569 during placebo exposure. The reported proportions are 0.298 and 0.200, and the unadjusted risk difference is 0.098, with a 95% confidence interval from 0.048 to 0.147. The registry reports an unadjusted p-value of <0.001. Together, these statistics describe a higher observed incidence of the endpoint during VIT-45 exposure in the posted comparison.

That finding is limited to the outcome definition and the two 7-day study periods. It concerns participants with at least one treatment-emergent adverse event, not the total number of events, their severity, or their clinical consequences. “Treatment-emergent” describes when an event was recorded in relation to treatment; it does not by itself establish that treatment caused the event. The separately listed serious-event and death counts provide additional safety information but do not resolve causality.

The study used a randomized, double-blind crossover design, with participants assigned to receive VIT-45 and placebo in different sequences. The registry’s posted comparison is unadjusted, and the record does not explain how within-participant pairing, study period, or sequence was handled in an inferential model. That uncertainty limits interpretation of the confidence interval and p-value as a complete crossover analysis.

The results do not establish event rates beyond the specified periods, long-term safety, or effects on anemia. The registry’s primary objective was safety and tolerability, and it posts no secondary outcome measures. It does not report a complete statistical analysis plan, missing-data methods, or analysis populations. These limits mean the findings should be understood as a summary of the registry’s posted outcome, rather than a complete account of every planned analysis or every clinically relevant outcome.

Nothing in the counts alone determines whether an individual should receive a treatment. The statistical result describes observed group-level event proportions and their estimated contrast; it does not make a treatment recommendation or establish a causal explanation for each event.

16. Why This Trial Matters Statistically

This trial is statistically notable because it combines a randomized, double-blind, placebo-controlled design with a crossover schedule. Such a design can make within-participant comparisons possible in principle, since participants were scheduled to receive both VIT-45 and placebo. At the same time, it makes the analysis structure important: outcomes from the same person may be related, and the two periods may differ. The registry reports an unadjusted comparison but does not describe whether the analysis modeled those features.

The endpoint is a participant-level binary outcome, which makes the reported counts and proportions relatively direct to interpret. The risk difference expresses the absolute contrast between the posted proportions, and its confidence interval communicates uncertainty around that contrast. The reported p-value adds a test-based summary, but neither a p-value nor a confidence interval can compensate for an unclear analysis method or missing reporting details.

The record also illustrates the distinction between statistical significance and clinical interpretation. The unadjusted confidence interval lies above zero and the reported p-value is <0.001, but the endpoint combines any treatment-emergent adverse event. Event severity, consequences, causal attribution, and events beyond the 7-day periods are not captured by that single contrast. The separate safety counts add context, while remaining limited summaries.

Finally, planning calculations based on the observed effect show how required sample sizes depend on the effect a future study aims to detect. They are illustrations under stated assumptions, not evidence about the power of this completed trial. The original sample-size rationale and more complete analysis details are not reported in the registry record. Recognizing both the information in the posted statistics and the limits of the record is central to sound interpretation.

17. 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 reports outcome counts for each treatment exposure but does not explain why the denominators are 584 and 569 when total enrollment is 594. It does not provide participant flow, the number completing each period, reasons for missing outcome information, or details about withdrawals. The extent to which incomplete follow-up affected the posted endpoint therefore cannot be determined.

Although the study is identified as a crossover, the posted comparison is unadjusted. The registry record does not state whether the statistical analysis accounted for within-participant correlation, treatment sequence, period effects, or carryover. It also does not provide an analysis plan or a detailed definition of the analysis population. These omissions prevent assessment of how well the reported inferential statistics align with the crossover structure.

The primary endpoint covers a 7-day period and includes any treatment-emergent adverse event. The registry does not give event-level detail for this endpoint, such as duration, severity, or causal assessment. Secondary outcomes are not posted, and there are no listed analysis entries. The original sample-size justification, interim analyses, and multiplicity approach are not reported in the registry record.

The serious adverse-event information is aggregated across treatment on Day 0 or Day 7, and the record does not establish treatment causality for the listed events or death. As a result, these figures offer a limited safety summary rather than a complete characterization of comparative risk. The findings should be interpreted within these reporting and follow-up limits.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Tolerability of Intravenous VIT-45 in Patients With Iron Deficiency Anemia — NCT00740246.
• Registry record last updated 2025-04-18; status last verified 2025-04.
• Results first posted 2025-04-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

This completed Phase 3 study was randomized, double-blind, placebo-controlled, and crossover in design. It enrolled 594 participants with iron deficiency anemia and compared sequences of intravenous VIT-45 and placebo on Day 0 and Day 7. The registry lists the study start as 2005-07 and primary completion as 2006-02.

The primary outcome was the number of participants with at least one treatment-emergent adverse event during each 7-day study period. The posted counts were 174 of 584 for VIT-45 and 114 of 569 for placebo. The unadjusted risk difference was 0.098, with a 95% confidence interval from 0.048 to 0.147 and an unadjusted p-value of <0.001. The registry reports serious-event and other safety counts, but does not describe a crossover-adjusted analysis, missing-data methods, or the original sample-size rationale.