Peritoneal Dialysis vs Furosemide for Acute Kidney Injury After Cardiopulmonary Bypass: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Peritoneal Dialysis vs Furosemide for Acute Kidney Injury After Cardiopulmonary Bypass (NCT01709227), a randomized na study. The primary outcome is Number of Participants With Negative Fluid Balance on Postop Day 1.

2. Clinical Question

The study addresses an early fluid-balance question in the setting of acute kidney injury after cardiopulmonary bypass. The registry summary describes oliguria after bypass and notes that PD and furosemide have both been used to attain negative fluid balance. It also states that the investigators intended a prospective comparison and hypothesized superior outcomes with PD. The primary outcome is narrower than the broad phrase superior outcomes: it records whether a participant had negative fluid balance on postoperative day 1.

The results report 21 participants with this outcome among 32 in the furosemide arm and 29 among 41 in the PD arm. The estimated risk difference for PD relative to furosemide is 0.051. Its confidence interval, from -0.165 to 0.267, includes no difference as well as effects in either direction. The posted unadjusted p-value is 0.641. These results do not provide precise evidence that one assignment produced a different rate of negative fluid balance on the measured day.

The question is about assignment to these trial arms and the recorded endpoint. It is not a comparison of every aspect of kidney recovery, longer-term health, or all possible approaches to fluid management. The registry record does not report a detailed eligibility definition or additional population characteristics.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. Enrollment was 73, with 32 participants in the furosemide arm and 41 in the PD arm. The trial status is completed. Its listed start is 2011-10 and its primary completion is 2015-06. The sponsor is Children's Hospital Medical Center, Cincinnati. The phase is listed as NA.

Random allocation supports a comparison based on assigned treatment, but the registry record does not report the sequence-generation method, allocation concealment, or whether randomization was stratified. It also does not report a protocol-level description of the analysis population. Because masking is listed as none, the trial was unmasked; the registry does not specify which people involved in treatment, outcome assessment, or analysis knew assignment.

The arms differed in both treatment and delivery. The furosemide arm received an initial intravenous regimen of 1 mg/kg every 6 hours for 2 doses, followed by management directed by the CICU attending. The PD arm used a standardized initial dialysis plan, with subsequent management directed by the CICU attending and Nephrology service. The registry record therefore describes initial treatment procedures but not a fully fixed course for all participants.

The primary outcome was a participant count for negative fluid balance on postoperative day 1. Secondary outcomes listed in the record include respiratory support, NGAL concentration, duration of cardiac ICU stay, duration of hospital stay, all-cause mortality, renal or electrolyte abnormalities, doses of potassium chloride or arginine chloride required, and B-natriuretic peptide. Nine secondary outcomes are posted. A detailed analysis plan, the intended hierarchy among outcomes, and original sample-size assumptions are not reported in the registry record. The planning figures associated with the posted effects are separate illustrations, not evidence about the trial's original design.

The design information establishes the randomized comparison and the treatment arms, but it does not resolve how departures from assigned treatment, missing measurements, or changes in clinical management were handled. Such details are important when interpreting an unmasked trial in which further care was directed by clinical teams.

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:

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 Number of Participants With Negative Fluid Balance on Postop Day 1, measured over Postop day 1.

The primary endpoint counts participants with negative fluid balance on postoperative day 1. The registry defines fluid balance using the difference between inputs and outputs, including urine output and PD drainage. The reported result is a count in each arm, rather than a continuous measure of the amount of fluid gained or lost.

Fluid balance is relevant to the stated clinical question because the registry summary describes PD and furosemide as approaches used to attain negative balance when oliguria follows cardiopulmonary bypass. A binary endpoint makes the comparison a question about how many participants crossed the endpoint's negative-balance criterion, not how far each participant's balance was from zero. The precise operational rules for recording all inputs and outputs, the handling of borderline values, and any measurement procedures are not reported in the registry record.

The result is assessed at a specified early time point, postoperative day 1. It therefore describes a short-term fluid-balance outcome and does not, by itself, measure the duration of kidney injury, longer-term kidney function, or overall recovery. Other clinical and laboratory outcomes were listed as secondary endpoints, but a posted primary-outcome result should not be treated as a substitute for those separate measures.

The registry reports 21 participants with negative fluid balance among 32 assigned to furosemide and 29 among 41 assigned to PD. This count-based outcome allows the arm results to be expressed as risks and compared using a risk difference. The endpoint's binary form is convenient for a direct comparison, but it discards information about the magnitude of each participant's fluid balance.

7. Results Posted in the Registry

• Peritoneal Dialysis: 70.7% (29/41) versus 65.6% (21/32) on control; risk difference 5.1 percentage points (95% CI -16.5 to 26.7), risk ratio 1.08 (0.78–1.48); unadjusted two-proportion z-test p = 0.641.

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.

All Cause Mortality

• 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:
  • Peritoneal Dialysis: 2.4% (1/41) versus 9.4% (3/32) on control; risk difference -6.9 percentage points (95% CI -18.1 to 4.2), risk ratio 0.26 (0.03–2.38); unadjusted two-proportion z-test p = 0.196.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Peritoneal Dialysis and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning respiratory support, laboratory measurements, lengths of stay, mortality, renal or electrolyte abnormalities, and medication requirements. These outcomes cover aspects of care and clinical status beyond the primary fluid-balance measure. However, the record does not post comparative results for most of these listed outcomes. Without those estimates, a coherent pattern across secondary endpoints cannot be established.

All-cause mortality has posted counts and a comparison, but it is a distinct outcome from negative fluid balance on postoperative day 1. It does not validate or contradict the primary result, and its uncertainty should be considered on its own. The registry record does not provide a full analysis for the other secondary outcomes, including effect estimates, confidence intervals, or detailed comparisons. Results for those outcomes are not reported in the registry record.

Secondary outcomes can help describe whether an intervention's observed effects extend to other dimensions, but they do not replace the primary endpoint. They may also be exploratory or evaluated alongside multiple outcomes. In general, examining many outcomes increases the chance that some will look unusual by chance, especially when no adjustment or prespecified testing hierarchy is used. The registry record does not report a multiplicity plan, so unadjusted secondary findings carry less weight than a clearly prespecified primary comparison.

The available secondary information is therefore limited: the outcome list indicates what was of interest, while the posted results do not permit a broad assessment of consistency across that list. Absence of a posted comparative result is not evidence that the arms were identical on that outcome. It means the registry record does not provide enough information to estimate or interpret the between-arm difference.

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

• Respiratory Support Administered
• NGAL Concentration
• Duration of Cardiac ICU Stay
• Duration of Hospital Stay
• All Cause Mortality
• Renal/Electrolyte Abnormalities
• Doses of Potassium Chloride or Arginine Chloride Required
• B-Natriuretic Peptide

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is a comparison of a binary outcome: each participant either did or did not have negative fluid balance on postoperative day 1. For a binary endpoint, the risk in an arm is the number with the event divided by the number in that arm. The registry reports 21 of 32 for furosemide and 29 of 41 for PD, along with arm risks of 0.656 and 0.707. These are two ways of describing the same arm-level outcome.

What does the risk difference express?

The risk difference subtracts the comparator-arm risk from the intervention-arm risk. In this comparison, the estimated difference for PD relative to furosemide is 0.051. A value of zero would mean equal risks on this scale. A positive estimate indicates a higher observed risk in the PD arm; a negative estimate would indicate a lower observed risk. The sign describes direction, while the size describes the estimated absolute separation between arm risks. It is not a relative change.

Other scales answer related but differently worded questions. The relative risk compares one arm's risk with the other arm's risk, and the odds ratio compares their odds. The registry reports a relative risk of 1.078 and an odds ratio of 1.266. Because these are transformations of the same outcome counts, they should not be treated as separate replications. The risk difference is often straightforward for communicating absolute separation, while relative measures can be useful when the comparison is framed proportionally. None of these measures removes the uncertainty caused by limited data.

How should the confidence interval be read?

A confidence interval describes the range of effect estimates that are compatible with the data under the interval's statistical procedure. In general, a narrower interval indicates greater precision and a wider interval indicates less precision. The primary interval is -0.165 to 0.267. It includes zero and allows values on both sides of zero, so the data do not pin down the direction of the underlying risk difference. The registry record does not report the specific procedure used to construct the primary confidence interval.

In general, a p-value measures how unusual the observed data, or data more extreme, would be under a specified null model and test procedure. The unadjusted primary p-value is 0.641. It is not the probability that the null hypothesis is true, nor does it quantify the chance that the result will replicate. The registry identifies this value as unadjusted, and the detailed testing procedure is not reported in the registry record.

Why do the counts matter?

Binary estimates are based on how many participants had the event and how many did not. With limited counts, moving the classification of a participant can change an arm's risk and the estimated difference. In general, less information tends to produce less precise estimates, which is reflected in wider confidence intervals. The uncertainty in the posted interval should therefore remain central to interpretation; the point estimate by itself is not a complete summary.

Randomization creates the design basis for comparing assigned groups, but it does not guarantee that every realized group characteristic is identical. The registry record does not provide baseline characteristics or adjusted analyses. It also does not report whether the primary comparison followed an intention-to-treat, per-protocol, or other analysis population. The arm denominators in the posted result are the denominators to use when describing these reported counts; the handling of missing endpoint data is not reported in the registry record.

What does unadjusted mean in this comparison?

An unadjusted comparison uses the outcome information without a reported correction for multiple testing or an adjustment for other variables. It is not possible to assume that the p-value accounts for the number of outcomes examined. The record lists numerous secondary outcomes, but the multiplicity strategy and any prespecified testing order are not reported. As a result, isolated secondary findings, especially when considered after examining several outcomes, generally warrant more caution than a prespecified primary comparison.

Statistical significance and clinical importance are distinct concepts. A p-value addresses evidence against a null model under a test; it does not tell whether a difference is meaningful in clinical practice. A confidence interval can help show the range of differences compatible with the data, but the registry record does not state a threshold for a clinically important effect. No such threshold should be inferred from the observed estimate.

What do the planning calculations represent?

Planning calculations use assumptions about an effect to estimate how many participants might be needed for a specified power under a stated statistical model. In general, power is the probability of detecting an assumed effect under that model if the effect is present. The posted planning figures use the observed effect, and also fractions of that observed effect, under a two-sided significance level of 0.05, equal allocation, and a normal approximation. These are planning illustrations rather than a reconstruction of the original design. The registry's original sample-size justification and design assumptions are not reported in the registry record.

These statistical summaries address different questions: the risk difference estimates absolute separation, the confidence interval conveys precision, and the p-value measures evidence under a null model and test. None alone establishes causality beyond the randomized comparison, makes the arms equivalent, or answers outcomes that were not measured or reported.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.051 for PD relative to furosemide, with a confidence interval from -0.165 to 0.267. The interval crosses zero, so the data are compatible with no difference and with a range of effects in either direction. Its width indicates that the estimate is not precise enough to distinguish modest differences from larger ones confidently. The endpoint counts are 21 of 32 in the furosemide arm and 29 of 41 in the PD arm.

In general, a confidence interval is an uncertainty summary for an estimated effect under a statistical procedure. It should not be read as a range containing every possible true effect or as a probability statement about the particular effect. A confidence interval that includes zero does not prove the treatment effects are equal; it indicates that zero is among the values compatible with the data at the interval's stated confidence level. The confidence level and the exact interval method are not reported in the registry record.

The relative risk estimate is 1.078, with an interval from 0.784 to 1.483. The odds ratio estimate is 1.266, with an interval from 0.469 to 3.415. Their intervals also include the null value on their respective scales. These alternative measures do not make the evidence more precise; they re-express the same binary outcome counts. The absolute risk difference remains a direct way to describe how separated the observed arm risks are.

The secondary mortality estimate is also imprecise: its risk difference is -0.069, with an interval from -0.181 to 0.042. The small number of recorded deaths makes a firm directional conclusion inappropriate. More broadly, the registry record does not report confidence intervals for the other listed secondary outcomes, and those outcomes cannot be assigned precision estimates from the posted information.

Precision concerns the uncertainty around an estimate, not whether its point estimate favors one arm. The main statistical message is that the primary estimate has substantial uncertainty, including plausible values on both sides of no difference. The posted results therefore do not support a precise claim about the size or direction of the underlying primary effect.

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 expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total sample sizes and are not total event counts. The calculation uses a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. For each planning scenario, the assumed effect is the observed effect or a stated fraction of it. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to detect the selected effect with 80% power under its assumptions. The 90% power column applies the same idea with a higher target probability of detecting that assumed effect. These are hypothetical design calculations, not descriptions of the enrollment or a measure of how much power the completed trial actually achieved.

The figures increase as the assumed effect becomes smaller: planning for 75% of the observed effect requires more participants than planning for 100% of it, and planning for 50% requires more again. This follows the general principle that smaller differences are harder to distinguish from random variation, so more participants are needed to detect them at a given power and significance level.

The sample-size figures are planning illustrations computed from the observed effect, not observed power. They depend on their assumptions and should not be read as proof that the original trial was designed around those assumptions. The registry record does not report the original target enrollment, anticipated event rates, attrition allowance, or other design inputs.

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 = 0.656; treatment proportion p₁ = 0.707; average p̄ = 0.682.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6587 = 1.2911.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6577 = 0.5536.
4. n = (1.2911 + 0.5536)² / (0.0511)² = 1,304.8, rounded up to 1,305 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 <- 0.65625                          # control proportion
p1 <- 0.707317073170732                          # 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(1709227)
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 = 1,305 (80% power), 1,747 (90% power)
 75% of observed effect: n per arm = 2,345 (80% power), 3,139 (90% power)
 50% of observed effect: n per arm = 5,331 (80% power), 7,136 (90% power)
power.prop.test: 1304.8 
Simulated power at n = 1,305 per arm: 0.799 (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. Multiplicity, Missing Data and Analysis Populations

The record lists a primary endpoint and multiple secondary outcomes, but does not report a multiplicity strategy. It is not reported in the registry record whether the primary endpoint was the only confirmatory test, whether secondary outcomes had a prespecified order, or whether any adjustment for testing multiple outcomes was planned. Without this information, the unadjusted p-values should not be interpreted as if they necessarily controlled the overall chance of a false-positive finding across all outcomes.

The record's listed analyses do not include a detailed sponsor-reported statistical analysis, and it does not describe interim analyses or stopping rules. These details are not reported in the registry record. No assumptions about interim monitoring, data-dependent decisions, or prespecified subgroup analyses should be made.

Missing-data procedures are also not reported. The posted primary counts have arm denominators of 32 and 41, but the record does not say whether every randomized participant had a measured primary outcome, how unavailable measurements were handled, or whether any participants were excluded from the analysis. It does not report an intention-to-treat, modified intention-to-treat, or per-protocol population. The difference between enrolled participants and those included in any particular endpoint analysis cannot be assessed from the record.

Likewise, no information is reported about adherence to assigned treatment, crossover, treatment discontinuation, or deviations from the planned initial approaches. These matters can be relevant to interpreting an assignment-based randomized comparison, especially because further management was directed by clinical teams. The registry record does not provide enough detail to determine their frequency or their handling in analysis.

The absence of these details does not show that appropriate procedures were absent; it means they cannot be verified from the registry record. A fuller protocol and statistical analysis plan would be needed to evaluate prespecification, missing-data assumptions, the target analysis population, multiplicity control, and whether the reported outcome comparisons followed the intended plan.

15. 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 non-serious adverse event terms

The registry reports zero serious adverse events among 32 participants at risk in the furosemide arm and zero among 41 participants at risk in the PD arm. For adverse events not classified as serious, it reports zero affected participants in the furosemide arm and 2 in the PD arm. The listed death counts are 3 in the furosemide arm and 1 in the PD arm.

These are participant counts, not event rates adjusted for exposure time. The registry does not provide serious-event terms, since none are listed, and it does not describe the nature or severity of the 2 other adverse events. It also does not state whether the adverse-event categories overlap with deaths or with other outcomes. The mortality endpoint is reported separately as all-cause mortality during hospitalization, so those counts should not be treated as a cause-specific safety comparison.

Zero recorded serious events in these groups does not establish that serious harms cannot occur. With limited enrollment and no detailed event descriptions, the safety information is descriptive and cannot precisely compare uncommon harms. The registry record does not provide additional safety analyses or a detailed method for event collection and attribution.

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

The primary result describes the proportion of enrolled participants in each randomized arm who had negative fluid balance on postoperative day 1. The observed risk difference favors a higher recorded proportion in the PD arm, but its confidence interval includes zero and extends in both directions. The evidence is therefore uncertain about the direction and size of the underlying difference. The unadjusted p-value does not show a statistically clear separation under the posted comparison.

This does not mean that the two treatments have been shown to be equivalent. Equivalence requires a defined margin and a design and analysis intended to determine whether effects fall within that margin; no such margin or equivalence analysis is reported in the registry record. Nor does the result show that either approach is ineffective. It describes one endpoint at an early time point in a particular randomized comparison.

Negative fluid balance is not the same as a complete assessment of kidney recovery or overall clinical outcome. The registry lists other outcomes, but most do not have posted comparative results. The mortality comparison is also uncertain and is not sufficient to establish a difference in deaths. The available data cannot support a broad claim of superiority across outcomes.

Randomization is an important feature because it establishes an intended comparison of assigned treatments. Interpretation still depends on how participants were analyzed, whether outcomes were missing, and how treatment deviations were handled; these details are not reported in the registry record. The unmasked design and clinician-directed further management also form part of the context in which the observed results were generated, without by themselves determining the direction of bias.

The appropriate reading is limited: the registry records the arm counts and an imprecise estimated difference for the primary fluid-balance outcome. It does not establish a precise benefit, harm, or equivalence, and it does not answer questions about outcomes for which comparative results are unavailable.

17. Why This Trial Matters Statistically

This trial illustrates why an estimated effect and its precision need to be read together. The primary point estimate is on the PD-favoring side of zero, but its confidence interval includes zero and allows effects in either direction. Focusing only on the direction of the point estimate would overstate what the data resolve; focusing only on a p-value would omit the range of effects compatible with the result.

The outcome is binary even though fluid balance is measured from quantities of inputs and outputs. Counting participants with negative balance provides a clear threshold-based comparison, but it does not preserve information about how negative or positive each participant's balance was. Endpoint definitions and measurement procedures can therefore matter as much as the choice of statistical scale. Details about those procedures are not reported in the registry record.

The posted planning illustrations also demonstrate how sample-size needs depend on the effect a study is intended to detect. Smaller assumed effects require more participants under the stated planning assumptions. Such calculations are useful for planning, but calculations based on an observed effect do not reveal the trial's original design rationale or the probability that the completed trial detected its true effect.

Finally, a registry may list numerous outcomes while reporting detailed comparative information for only some of them. That distinction matters statistically: outcome lists identify intended areas of interest, but without estimates and uncertainty measures they cannot show whether effects are consistent. The lack of a reported multiplicity strategy and analysis population further limits the strength of conclusions that can be drawn from isolated secondary results.

18. 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 reported enrollment is limited to 73 participants, and the primary comparison has a wide confidence interval. The estimate is consequently uncertain and should not be treated as a precise measure of the difference between arms. The population is specifically described as infants or neonates with oliguria after cardiopulmonary bypass; the registry record does not provide enough detail to determine how well the results apply to other populations or clinical settings.

The trial was unmasked, and subsequent management in both arms could be directed by the CICU attending; PD management also involved the Nephrology service. The record does not describe the extent of treatment adherence, crossover, or differences in co-interventions. These features limit assessment of how closely participants' care followed the initial arm assignments.

The primary endpoint concerns negative fluid balance on postoperative day 1. Its definition refers to inputs and outputs, including urine output and PD drainage, but detailed measurement rules and missing-measurement procedures are not reported. The endpoint captures whether balance was negative rather than the magnitude of fluid balance, and it is not a direct measure of longer-term kidney status.

Comparative results are not posted for most secondary outcomes, and the record does not report a multiplicity plan, analysis population, covariate-adjusted model, or detailed statistical analysis plan. Original sample-size assumptions, interim analyses, and the handling of missing data are also not reported in the registry record. The safety information gives counts but little detail about event type or attribution. These gaps constrain both replication and evaluation of the robustness of the reported comparisons.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Peritoneal Dialysis vs Furosemide for Acute Kidney Injury After Cardiopulmonary Bypass — NCT01709227.
• Registry record last updated 2017-06-09; status last verified 2017-05.
• Results first posted 2017-06-09.
• 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.

22. Record Summary

NCT01709227 is a completed randomized, parallel-group, unmasked trial comparing furosemide with peritoneal dialysis in infants with oliguria after cardiopulmonary bypass. Enrollment was 73. The primary outcome was the number of participants with negative fluid balance on postoperative day 1.

The registry reports 21 of 32 participants with the primary outcome in the furosemide arm and 29 of 41 in the PD arm. The risk-difference estimate for PD is 0.051, with a confidence interval from -0.165 to 0.267 and an unadjusted p-value of 0.641. The interval includes no difference and effects in either direction, leaving the estimated difference imprecise.

All-cause mortality is posted as a secondary outcome, while comparative results for most listed secondary outcomes are not reported in the registry record. Serious adverse events were recorded for zero participants in either arm; other adverse events and deaths are reported as participant counts. The original sample-size assumptions, analysis population, missing-data procedures, and multiplicity plan are not reported in the registry record.