Deferoxamine for the Prevention of Cardiac Surgery-Associated Acute Kidney Injury: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Deferoxamine for the Prevention of Cardiac Surgery-Associated Acute Kidney Injury (NCT04633889), a randomized phase 2 study. The primary outcome is Acute Kidney Injury.

2. Clinical Question

The trial asks whether prophylactic deferoxamine is associated with a different incidence of acute kidney injury after cardiac surgery than placebo. The registry describes a phase 2, randomized, double-blind, placebo-controlled trial and identifies acute kidney injury as the primary outcome, assessed over 7 days. Its rationale is that iron may contribute to kidney injury, and cardiac surgery involving cardiopulmonary bypass can involve hemolysis. That rationale motivates the question; it is not itself evidence of an effect in trial participants.

The posted comparison is based on participants with an acute kidney injury event in each group. The registry reports 99 of 151 participants in the deferoxamine arm and 108 of 150 in the placebo arm. The unadjusted recalculation estimates a risk difference of -0.064, with an interval from -0.169 to 0.040. The estimate is numerically below zero, but the interval includes zero, so the posted results do not precisely establish the direction or size of a difference.

3. Trial Design

The registry identifies NCT04633889 as a completed phase 2 trial sponsored by Brigham and Women's Hospital. It lists randomized allocation, triple masking, and a parallel-group model. The trial record gives enrollment as 320. The primary endpoint results are posted for 151 participants assigned to deferoxamine and 150 assigned to placebo; the reasons for the difference between the enrollment figure and these endpoint denominators are not reported in the registry record.

The intervention was deferoxamine by intravenous infusion over 12 hours, at 30mg/kg up to a maximum dose of 6g. The placebo was a normal saline infusion over the same stated duration. The brief summary describes the study as double-blind, while the design fields identify triple masking. Further details about which people were masked are not reported in the registry record.

The trial started on 2021-04-13, reached primary completion on 2024-08-26, and is marked completed. These dates describe the record's trial timeline; they do not, by themselves, describe when results were analyzed or posted. The registry's primary outcome is acute kidney injury within 7 days, defined by a composite of urine output, serum creatinine, or renal replacement therapy criteria.

The record lists 11 outcome measures and 10 secondary outcomes. It includes numeric results for the primary outcome and for three secondary outcomes in the available results information. Numeric results for the remaining listed secondary outcomes are not reported in the registry record. The original design's sample-size rationale, allocation procedure details, and full statistical analysis plan are 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: The discrepancy between the number of patients enrolled (n=320) versus the number randomized, dosed, and included in the final analysis (n=301) was due to some patients being withdrawn from the study after enrollment but prior to randomization.

Overall Study

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 Acute Kidney Injury, measured over 7 days.

The primary endpoint is the number of participants meeting the trial's composite definition of acute kidney injury within 7 days. A participant meets the definition if any listed criterion occurs: urine output <0.5 ml/kg/h for ≥6 consecutive hours within the first 48h or until the Foley catheter is removed, whichever occurs first; an increase in serum creatinine ≥0.3 mg/dl within the first 48h; an increase in serum creatinine ≥50% within 7 days; or receipt of renal replacement therapy within 7 days.

A composite endpoint combines multiple events into one outcome. In general, this can capture more than one clinically relevant way the condition may present, while the resulting summary does not show which component accounts for the overall group result. Component-specific primary outcome counts are not reported in the registry record, so the posted composite comparison cannot establish which criterion contributed most to the event totals.

The endpoint is recorded as participants with an event, rather than as a continuous measurement. That makes the primary comparison a comparison of event risks between randomized groups. The 7-day timeframe also defines the period covered by the primary outcome; it does not describe longer-term kidney outcomes.

7. Results Posted in the Registry

• Deferoxamine: 65.6% (99/151) versus 72.0% (108/150) on control; risk difference -6.4 percentage points (95% CI -16.9 to 4.0), risk ratio 0.91 (0.78–1.06); unadjusted two-proportion z-test p = 0.228.

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 Postoperative Myocardial Injury

• 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:
  • Deferoxamine: 9.9% (15/151) versus 10.0% (15/150) on control; risk difference -0.1 percentage points (95% CI -6.8 to 6.7), risk ratio 0.99 (0.50–1.96); unadjusted two-proportion z-test p = 0.985.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferoxamine and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Atrial Fibrillation or Atrial Flutter

• 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:
  • Deferoxamine: 32.4% (33/102) versus 35.6% (32/90) on control; risk difference -3.2 percentage points (95% CI -16.6 to 10.2), risk ratio 0.91 (0.61–1.35); unadjusted two-proportion z-test p = 0.640.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferoxamine and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Prolonged Mechanical Ventilation

• 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:
  • Deferoxamine: 20.5% (31/151) versus 18.0% (27/150) on control; risk difference 2.5 percentage points (95% CI -6.4 to 11.4), risk ratio 1.14 (0.72–1.81); unadjusted two-proportion z-test p = 0.578.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferoxamine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes with numeric results in the registry record cover postoperative myocardial injury, atrial fibrillation or atrial flutter, and prolonged mechanical ventilation. Across these outcomes, the unadjusted recalculations do not provide a consistent pattern of clear group separation: the point estimates vary in direction and the reported intervals include their respective null values. This broad pattern does not add a definitive secondary finding that changes the interpretation of the primary comparison.

These results are related to the primary outcome in that they describe other postoperative outcomes in the same trial, but they address distinct questions and timeframes. They do not validate or negate the primary composite result. The registry lists 10 secondary outcomes, while numeric results for the other listed outcomes are not reported in the registry record. The available numeric results should not be treated as a complete account of every secondary question.

Unadjusted secondary comparisons carry less weight when many outcomes are examined. In general, evaluating multiple outcomes increases the chance that some results appear unusual by chance, even if there are no underlying differences. Adjustment for multiplicity, hierarchy among outcomes, and which analyses were prespecified are not reported in the registry record. Without that information, secondary p-values and intervals are best regarded as exploratory descriptions rather than as independent confirmatory evidence.

The reported secondary findings should also be interpreted in light of their available denominators and uncertainty. The record does not explain why denominators differ for some secondary outcomes, nor does it report missing-data procedures. These limitations prevent a complete assessment of how the secondary analyses relate to the randomized groups.

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

• Renal Tubular Injury
• Number of Participants With Major Adverse Kidney Events
• Number of Participants With Postoperative Myocardial Injury
• Number of Participants With Atrial Fibrillation or Atrial Flutter
• Number of Participants With Prolonged Mechanical Ventilation
• Time to Liberation From Vasoactive Medications
• Number of Participants With Sepsis
• Ventilator-free Days

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each person either met the acute kidney injury definition during the stated timeframe or did not. For a binary outcome, an event risk is the proportion of participants in a group who experienced the event. The posted arm counts provide the event numerators and denominators used for the unadjusted recalculation.

What does the risk difference mean?

The risk difference subtracts the placebo event risk from the deferoxamine event risk. Its scale is an absolute difference in risk. The posted estimate is -0.064, with an interval from -0.169 to 0.040. The negative point estimate reflects fewer observed events relative to the group denominator in the deferoxamine arm, but the interval includes zero. In general, zero is the no-difference value for a risk difference. An interval extending across zero signals uncertainty about the direction as well as the magnitude of the difference.

How do the risk ratio and odds ratio differ?

The risk ratio compares the event risks directly; its null value is one. The odds ratio compares event odds rather than event risks, and its null value is also one. The recalculated estimates are 0.911 for the risk ratio and 0.740 for the odds ratio. Their respective intervals, 0.782 to 1.061 and 0.454 to 1.208, include one. These measures can differ numerically because they use different scales, especially when events are common. They should not be read as interchangeable quantities.

What does the p-value test?

The registry reports a chi-squared analysis with p = 0.23. The unadjusted recalculation gives p = 0.228. In general, a p-value describes how unusual data at least as incompatible with a null hypothesis would be if that null model and the test assumptions were correct. It is not a measure of the probability that the null hypothesis is true, nor does it indicate the probability that a result will replicate. The posted p-values do not establish a difference under conventional significance testing, but that is not equivalent to proving that the groups are identical.

The chi-squared test is a method for comparing categorical outcome distributions. It is suitable in general for comparing observed counts with counts expected under a null model, subject to its assumptions. The registry does not report further details about the sponsor's test implementation or any adjustment variables. The recalculated comparison is unadjusted and uses the posted summary counts; it does not reproduce an adjusted or participant-level analysis.

Why do intervals matter?

A confidence interval is a range of effect values compatible with the data under a specified statistical procedure. It conveys precision as well as direction: a narrower interval indicates greater precision than a wider interval, while an interval spanning the null value leaves the direction unresolved. The registry record does not state the confidence level for the recalculated intervals. The interval should therefore be interpreted by its endpoints and its relation to the null value, without assigning it an unreported confidence level.

For this primary result, the risk-difference interval spans negative and positive values. This means the data are not precise enough to exclude either a reduction or an increase in event risk on that scale. It does not mean that every value in the interval is equally plausible, and it does not describe uncertainty from design limitations or missing data. It is a measure of sampling uncertainty under the recalculation's assumptions.

What is and is not recalculated?

The recalculated measures are simple unadjusted comparisons derived from the posted summary counts. They are not a reconstruction of the full trial analysis, and they do not incorporate participant-level information, covariates, or any analysis choices not contained in the summary data. The record does not report whether the sponsor used adjusted analyses, how missing observations were handled, or which analysis population was used. Such details cannot be inferred from the count comparison.

Randomization is intended in general to make treatment groups comparable at assignment, but it does not guarantee that every observed characteristic is balanced in a finite sample. The record does not provide baseline characteristics in the registry record used for this analysis. No claim about baseline balance or adjustment can therefore be made. Likewise, masking is listed as triple in the design fields, but the identities of masked parties and the procedures for maintaining masking are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.064, and its interval runs from -0.169 to 0.040. Because the interval includes zero, the posted results do not distinguish clearly between a reduction in event risk, no difference, and an increase. The interval is wide enough to leave meaningful uncertainty about both the direction and size of the effect. The registry record does not report the confidence level attached to this recalculated interval.

On the relative scales, the risk-ratio estimate is 0.911, with interval 0.782 to 1.061, and the odds-ratio estimate is 0.740, with interval 0.454 to 1.208. Each interval includes one, the null value for its measure. These intervals are also unadjusted recalculations from the posted summary counts. They do not substitute for a sponsor analysis that may use additional information or a different method.

Precision concerns how tightly the data locate an effect, not whether an effect is important. A p-value above a common significance threshold does not show that the effect is exactly zero. Conversely, a point estimate below zero does not establish a benefit when uncertainty includes values in the other direction. The original design's target precision and clinically meaningful effect are not reported in the registry record, so the observed interval cannot be judged against a stated design target.

There is also uncertainty not captured by a sampling interval. The registry record does not report the handling of missing outcome data, analysis-population definitions, or component-specific primary outcome counts. Those omissions limit assessment of how the analysis reflects all randomized participants and what drives the composite result.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the binary outcomes in the sample-size section. They are not total event counts. The planning assumptions stated for these illustrations are a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect. The original trial's own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under which a study would have an 80% chance of detecting the specified effect if that effect and the planning assumptions were correct. The 90% power column gives the corresponding planning target for a 90% chance. These are design calculations, not guarantees about a future study's result. The figures are conditional on the stated assumptions and the effect used for the row.

The rows that use 100%, 75%, and 50% of the observed effect explore different effect sizes. Smaller effects require more participants to detect under the same assumptions, which is why the planning requirements increase as the assumed fraction becomes smaller. The sample-size curve expresses the same general relationship visually; it should be read as a planning aid rather than as a description of observed trial performance.

These figures are not observed power. Observed power calculated from the effect estimate after a study is complete does not add a useful independent summary of the result. The planning illustrations instead show how sample requirements depend on assumed effect size and design choices. They do not establish that the completed trial was underpowered or that a particular effect is true.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.720; treatment proportion p₁ = 0.656; average p̄ = 0.688.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6553 = 1.2844.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6537 = 0.5502.
4. n = (1.2844 + 0.5502)² / (-0.0644)² = 812.3, rounded up to 813 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 <- 0.72                          # control proportion
p1 <- 0.655629139072848                          # 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(4633889)
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 = 813 (80% power), 1,087 (90% power)
 75% of observed effect: n per arm = 1,425 (80% power), 1,907 (90% power)
 50% of observed effect: n per arm = 3,158 (80% power), 4,227 (90% power)
power.prop.test: 812.3 
Simulated power at n = 813 per arm: 0.803 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry's sponsor-reported primary analysis is a chi-squared test with p = 0.23. The unadjusted recalculation from the posted counts gives p = 0.228 and a risk difference of -0.064, with an interval from -0.169 to 0.040. The reported p-value and recalculated p-value are close in their displayed precision and lead to the same broad reading: the posted comparison does not establish a difference under conventional significance testing.

The recalculation is a simple unadjusted analysis of summary counts. It is not a replacement for the sponsor's analysis and does not reproduce any unreported analysis details. The record does not provide a fuller account of the sponsor's model, analysis population, missing-data handling, or adjustment strategy. Those features should not be assumed to match the recalculation.

The discrepancy flag is false, so the record does not identify a conflict between the sponsor analysis and the recalculation. The recalculated effect estimates and intervals remain useful for describing absolute and relative effect scales, but the sponsor's reported analysis is the trial's own posted inferential result. Neither the p-value nor the point estimate should be treated as proof that deferoxamine does or does not alter acute kidney injury risk.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary outcome and multiple secondary outcomes. It does not report whether the analysis plan controlled the family-wise error rate, used another multiplicity adjustment, or specified a hierarchy for interpreting outcomes. It is therefore not possible to determine from the record whether secondary comparisons were intended as confirmatory tests or as exploratory analyses. When several outcomes are tested, unadjusted results can produce apparently notable findings by chance; this is a general statistical concern, not evidence that any particular posted result is false.

The handling of missing outcome data is not reported in the registry record. The analysis populations are also not reported: it is not stated whether analyses followed an intention-to-treat approach, a per-protocol approach, or another definition. Reasons for differences between denominators across outcomes are not reported. For example, atrial fibrillation or atrial flutter results use denominators of 102 and 90, while the primary outcome uses 151 and 150. The record does not explain these differences, so they should not be attributed to a particular cause.

The original statistical analysis plan, covariate adjustment strategy, and interim-analysis procedures are not reported in the registry record. No assumptions about these procedures can be made from the posted endpoint results. The record also does not report component-level counts for the primary composite or the approach used to handle any participants who did not have all endpoint components assessed.

These reporting gaps do not change the posted counts, but they limit evaluation of the analysis choices and the potential influence of missingness or multiple testing. A reader can describe the posted comparisons and their uncertainty while recognizing that the registry information does not permit a full audit of the trial's analysis process.

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 0% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: vasoactive-inotropic score ≥30 (14.0%), infection/sepsis (7.9%), ards (2.0%), anaphylaxis (0.0%).

The registry reports serious adverse events affecting 23 of 151 participants in the deferoxamine group and 25 of 150 in the placebo group. Deaths are reported for 6 participants in each group. The record reports 0 other adverse events in each group. These figures describe the posted safety counts; they do not establish that an event was caused by the assigned infusion, and the record does not provide further causal assessment in the registry record.

The listed serious adverse-event terms include Vasoactive-Inotropic Score ≥30 at 14.0%, Infection/Sepsis at 7.9%, ARDS at 2.0%, and Anaphylaxis at 0.0%. The registry information does not specify the denominators or further detail associated with these listed percentages in the registry record. They should be read as the listed term values, not as a complete description of all adverse events or as a comparison of causal risk between groups.

Safety counts are not directly interchangeable with the primary efficacy endpoint. They summarize reported adverse events, whereas the primary endpoint is a composite of kidney injury criteria. The record does not provide enough detail to infer event timing, severity beyond the serious-event classification, or attribution to treatment.

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

The posted primary result shows fewer acute kidney injury events in the deferoxamine group than in the placebo group as a raw comparison of the reported counts. The recalculated risk difference is -0.064, but its interval extends from -0.169 to 0.040 and includes zero. The sponsor-reported chi-squared analysis gives p = 0.23. Taken together, these results leave substantial uncertainty about the direction and magnitude of any difference.

This result does not establish that deferoxamine prevents acute kidney injury, and it does not establish that the groups have identical risks. The p-value is not a probability that the treatment is ineffective. The point estimate is not a guarantee of the true effect. The interval indicates that the posted data are compatible with effects on either side of no difference under the recalculation method.

The endpoint is a composite that includes urine output, creatinine change, and renal replacement therapy criteria. Because component-specific primary results are not reported in the registry record, the overall outcome cannot show which part of the composite contributed to the event counts. The result is also limited to the defined 7-day timeframe; it does not report longer-term kidney outcomes.

The trial's phase, sample, and registry reporting should be considered when interpreting the result. The original sample-size justification, missing-data handling, analysis-population definition, and detailed statistical plan are not reported in the registry record. Numeric results for all listed secondary outcomes are likewise not reported. These constraints limit claims about precision, generalizability, and the broader balance of outcomes.

The appropriate statistical reading is descriptive and cautious: the posted comparison has a negative point estimate on the risk-difference scale, but the estimate is uncertain and the sponsor's reported test does not establish a statistically discernible difference. It is not a clinical recommendation or a conclusion about an individual's care.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment-effect estimate should be read together with its uncertainty. The primary point estimate is numerically below zero, but the interval spans zero and extends to a positive value. Looking only at event counts or only at the point estimate would give an incomplete account of what the data can support.

It also shows the value of identifying the effect scale. A risk difference expresses an absolute change in event risk, while risk and odds ratios express relative comparisons on different scales. The posted estimates do not all have the same numerical appearance, but their intervals include the null value for each measure. Choosing a measure should reflect the question being asked; one scale should not be treated as a substitute for all others.

Composite endpoints raise a further interpretive issue. They combine multiple criteria into a single outcome, which can summarize a broad clinical construct, but the overall count does not identify which component drives the result. Component-specific counts are not reported in the registry record. That makes it important to distinguish the evidence about the composite from evidence about any individual component.

Finally, planning calculations make explicit how sample requirements depend on the effect a future study aims to detect. Smaller assumed effects require larger planned samples under the stated assumptions. These illustrations are not observed power and do not recover the original design rationale, which is not reported. Together, these points support an interpretation centered on estimates, uncertainty, endpoint definition, and transparent reporting rather than on a single threshold.

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 primary analysis available for recalculation uses summary counts and is unadjusted. It cannot account for participant-level data, covariates, or analysis choices not reported in the registry. The sponsor reports a chi-squared p-value, but further details of the sponsor's analysis are not reported in the registry record.

The primary endpoint combines multiple criteria, and component-specific event counts are not reported. Consequently, the overall event comparison does not reveal whether the components showed similar patterns. The registry also does not report the original sample-size justification, a clinically important effect threshold, missing-data methods, or analysis-population definitions. The difference between the enrollment figure and the primary outcome denominators is not explained in the registry record.

Numeric results are available for only three of the listed secondary outcomes in the results information used for this analysis. The record does not report multiplicity procedures, endpoint hierarchy, or whether secondary analyses were prespecified as confirmatory. Denominators also vary for some secondary results, without an explanation in the registry record.

The trial is identified as phase 2, but the participant characteristics and detailed eligibility criteria are not reported in the registry record for this analysis. This limits assessment of how well the sample represents particular patient groups. The record's masking field says triple, while its brief summary describes a double-blind trial; further clarification of masking roles is not reported. Safety reporting also lacks detail on event timing and attribution. These limitations constrain interpretation of the posted results without changing the reported counts.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Deferoxamine for the Prevention of Cardiac Surgery-Associated Acute Kidney Injury — NCT04633889.
• Registry record last updated 2026-10-06; status last verified 2026-09.
• Results first posted 2026-01-26.
• 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

NCT04633889 is a completed randomized, parallel-group phase 2 trial sponsored by Brigham and Women's Hospital. The registry lists 320 participants enrolled and compares deferoxamine with normal-saline placebo by intravenous infusion over 12 hours. Its primary outcome is a composite acute kidney injury measure assessed within 7 days.

The primary outcome was recorded in 99 of 151 participants assigned to deferoxamine and 108 of 150 assigned to placebo. The unadjusted recalculation gives a risk difference of -0.064, with an interval from -0.169 to 0.040 and p = 0.228; the registry reports a chi-squared p-value of 0.23. The interval includes zero, leaving uncertainty about the direction and size of any difference.

The registry lists 10 secondary outcomes, but numeric results are not reported for all of them. The original design assumptions, missing-data procedures, analysis populations, and multiplicity approach are not reported in the registry record.