Acute Renal Failure Trial Network (ATN) Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Acute Renal Failure Trial Network (ATN) Study (NCT00076219), a randomized phase 3 study. The primary outcome is 60-day All-cause Mortality.

2. Clinical Question

3. Trial Design

The Acute Renal Failure Trial Network Study was a phase 3, randomized, parallel-group trial sponsored by the US Department of Veterans Affairs. The registry lists a start date of 2003-10 and primary completion in 2007-09; the study status is completed. It enrolled 1124 participants. The brief summary described a planned recruitment of 1164 patients over 3 years, 8 months, with active follow-up for 60 days. These are distinct statements in the record: the planned recruitment figure and the reported enrollment are not the same.

The trial compared two renal replacement therapy strategies. In the intensive group, intermittent hemodialysis and sustained low-efficiency dialysis were scheduled 6 times per week, while continuous venovenous hemodiafiltration was set at 35 mL/kg/hour. In the less-intensive group, the corresponding frequency was 3 times per week, and the continuous therapy rate was 20 mL/kg/hour. The trial was described as multicenter, prospective, randomized, and parallel-group. Masking is listed as none.

The primary outcome was the number of participants who died from any cause by day 60. The registry lists one posted outcome measure and one sponsor-reported analysis. Although the brief summary also names 60-day in-hospital mortality, 1-year all-cause mortality, and recovery of renal function by day 28 as secondary outcomes, no secondary outcomes are posted in the results summarized for the record. The registry record does not report further details of the allocation process, the analysis population, or other protocol procedures.

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

Analysis population for the primary outcome, as defined in the registry: Number of all-cause mortality by day 60

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 60-day All-cause Mortality, measured over 60 days.

The primary endpoint counts participants who died from any cause by day 60. It is a binary outcome for each participant: death by the specified time is counted as an event, and the reported group results give the number of events among the participants in each arm. The registry identifies the endpoint as 60-day all-cause mortality and describes the population as participants with all-cause mortality by day 60.

All-cause mortality is used because it captures deaths regardless of their attributed cause, rather than limiting the endpoint to deaths judged to arise from one particular condition or treatment. A fixed follow-up time also gives the comparison a defined horizon. The result should be read specifically as the count of deaths by day 60; it does not by itself describe when deaths occurred during follow-up or establish the cause of any individual death.

The summary states that the primary hypothesis anticipated a 10% reduction in 60-day all-cause mortality, from 55% in the conventional arm to 45% in the intensive arm. That statement describes the hypothesis in the summary, not the observed result. The posted endpoint counts are 302 of 563 participants in the intensive group and 289 of 561 in the less-intensive group. No secondary endpoint results are posted in the registry record.

7. Results Posted in the Registry

• Less-intensive Renal Replacement Therapy: 51.5% (289/561) versus 53.6% (302/563) on control; risk difference -2.1 percentage points (95% CI -8.0 to 3.7), risk ratio 0.96 (0.86–1.07); unadjusted two-proportion z-test p = 0.475.

8. Statistical Interpretation

9. Statistical Methods Explained

The outcome is binary because each participant either died by day 60 or did not. The posted arm results give the number of events and the number of participants in each group. For a binary outcome, a risk is the proportion of participants with the event in a group. The recalculated analysis compares these group risks using a risk difference. A risk difference is expressed on the same scale as the risks: it describes the absolute separation between the two group proportions, with the sign determined by the order of the groups in the comparison.

What does the risk difference describe?

The reported recalculation compares the less-intensive group with the intensive group. Its estimate is -0.021, with a 95% confidence interval from -0.080 to 0.037. The negative point estimate indicates a lower observed event proportion in the less-intensive group under that ordering. The estimate is not a guarantee about the underlying difference. It summarizes the observed data under the unadjusted calculation, while the interval conveys the uncertainty around that estimate.

Risk differences are often useful because they retain an absolute scale. A reader can interpret the estimate in relation to the group risks, rather than only as a relative comparison. The risk difference does not adjust for other variables. It is described as an unadjusted recalculation from the posted summary statistics, so it should not be mistaken for the sponsor's regression analysis.

What does the confidence interval add?

A confidence interval gives a range of estimates that are reasonably compatible with the data and the statistical method used, under the method's assumptions. In repeated use, a 95% confidence-interval procedure would cover the true parameter in 95% of such intervals. It is not a probability statement that the particular underlying effect has a 95% chance of lying in this one interval. The interval spans values below and above no difference, which means the data do not pin down the direction of the risk difference with precision.

The reported p-value for the recalculated risk difference is 0.475. A p-value measures how unusual data at least as incompatible with a specified no-difference model would be, if that model and the analysis assumptions held. It is not the probability that there is no difference, and it does not quantify the size or clinical importance of an effect. The value should be interpreted alongside the estimate and its interval, rather than on its own.

Why is the sponsor analysis a different method?

The sponsor reports logistic regression with an odds ratio of 1.09, a 95% confidence interval from 0.86 to 1.40, and p = 0.47. Logistic regression models the odds of the binary event and expresses the comparison on an odds-ratio scale. An odds ratio of 1 corresponds to equal odds in the groups. The registry record does not report the covariates, exact model specification, or analysis population for this regression, so those details cannot be assessed from the posted result alone.

An odds ratio is not the same measure as a risk difference. Odds compare the probability of an event with the probability of no event, while a risk is the event probability itself. The sponsor's estimate and the unadjusted risk-difference recalculation should therefore be read as results from distinct statistical approaches, not as interchangeable estimates. Their confidence intervals both include the value representing no group difference on their respective scales.

What assumptions matter for a binary-outcome analysis?

Unadjusted comparisons use the observed counts and group sizes without accounting for additional participant characteristics. Random assignment supports a comparison of groups, but does not eliminate uncertainty or ensure that every characteristic is balanced in the enrolled sample. The posted summary does not include participant-level data, so alternative adjusted analyses cannot be reconstructed from these counts. The registry record also does not report whether missing outcome data occurred or how it was handled.

The primary endpoint is a count of participants with an event, not a time-to-event analysis. The posted summary does not give event times, censoring information, or a survival analysis for mortality. As a result, the comparison addresses whether death occurred by day 60, rather than differences in the timing of death during the follow-up period. The available result is confined to that specified endpoint and follow-up horizon.

Finally, statistical non-significance is not evidence that the groups are equivalent. An equivalence conclusion requires a defined equivalence margin and a method designed to test whether the plausible difference lies within that margin. Such a margin and an equivalence analysis are not reported in the registry record. The appropriate interpretation is that the estimated difference is uncertain and that the available results do not establish a clear difference or establish equivalence.

10. Confidence Intervals and Precision

The recalculated risk difference is -0.021, with a 95% confidence interval from -0.080 to 0.037. This interval is important because it shows more than the point estimate: the data remain compatible with a range of possible differences, including no difference. Since the interval extends in both directions around zero, it does not identify a precise direction of the underlying group contrast.

The width of the interval reflects sampling uncertainty in the comparison. It should not be read as a range containing every possible true effect, nor as a statement that each value within it is equally likely. Rather, it is the uncertainty range generated by the specified calculation and its assumptions. The confidence level describes the long-run behavior of the interval method, not a probability assigned to the true effect after observing this trial.

The sponsor's odds ratio is 1.09, with a 95% confidence interval from 0.86 to 1.40. On the odds-ratio scale, the value corresponding to no difference is 1; the reported interval includes that value. The interval is consistent with odds in either direction relative to the other group, and the registry result alone does not establish which direction is more plausible. The sponsor's analysis and the recalculated risk difference use different effect scales, but each displays uncertainty that encompasses no difference.

Precision is distinct from statistical significance. A p-value alone cannot show whether an estimate is narrow enough to be informative, while the confidence interval displays the range of estimates compatible with the data under the method. The posted intervals leave uncertainty about the magnitude and direction of the comparison. They do not establish that the strategies have identical effects, and they do not support a precise estimate of a difference.

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 this binary outcome. They are not total event counts. The listed illustrations give participants per arm for 80% power and participants per arm for 90% power when planning around 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. For example, the figures for planning around 100% of the observed effect are 8,658 participants per arm for 80% power and 11,590 participants per arm for 90% power. The figures for planning around 75% are 15,384 and 20,595 per arm, respectively; for 50%, they are 34,594 and 46,310 per arm.

The 80% power column describes an illustrative design that would have an 80% chance of detecting the effect used in that calculation if the assumptions held and that effect were the true one. The 90% power column describes the corresponding design with a 90% chance. Higher planned power requires a larger sample under otherwise unchanged assumptions. Planning for a smaller effect also requires more participants, because a smaller separation between groups is harder to distinguish from sampling variation.

These calculations are illustrations based on the observed effect, not the trial's original design assumptions. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. This is not observed power. The registry record does not report the trial's original sample-size justification or its original design assumptions.

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 = 0.536; treatment proportion p₁ = 0.515; average p̄ = 0.526.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7062 = 1.3841.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7060 = 0.5942.
4. n = (1.3841 + 0.5942)² / (-0.0213)² = 8,657.9, rounded up to 8,658 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 <- 0.536412078152753                          # control proportion
p1 <- 0.515151515151515                          # 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(76219)
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 = 8,658 (80% power), 11,590 (90% power)
 75% of observed effect: n per arm = 15,384 (80% power), 20,595 (90% power)
 50% of observed effect: n per arm = 34,594 (80% power), 46,310 (90% power)
power.prop.test: 8657.9 
Simulated power at n = 8,658 per arm: 0.801 (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. Analyses Reported by the Sponsor

The sponsor-reported analysis uses logistic regression and reports an odds ratio of 1.09, a 95% confidence interval from 0.86 to 1.40, and p = 0.47. The recalculated analysis uses the posted arm counts to estimate an unadjusted risk difference of -0.021, with a 95% confidence interval from -0.080 to 0.037 and an unadjusted p-value of 0.475. These effect estimates are on different scales: the sponsor reports an odds ratio, while the recalculation reports a difference between risks.

Both analyses have intervals that include the value corresponding to no difference, and both p-values are close in their broad statistical interpretation. They should not be expected to match exactly because the methods and effect measures differ. The registry record does not report enough detail about the regression model to reproduce it from the arm-level counts. There is no flagged discrepancy between the posted results and the recalculation, so neither result is identified as conflicting with the other. The sponsor's regression remains the trial's own reported analysis; the recalculation is a simple unadjusted comparison of the posted summary counts.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one posted outcome measure and one sponsor-reported analysis. The brief summary names additional outcomes: 60-day in-hospital all-cause mortality, 1-year all-cause mortality, and recovery of renal function by day 28. However, no secondary outcome results are posted in the registry record summarized for this analysis. Their absence from the posted results means they cannot be interpreted alongside the primary endpoint.

When a study evaluates multiple outcomes or multiple analyses, the chance of at least one apparently positive result can increase if each is assessed without regard to the others. Methods for handling multiple comparisons, such as a prespecified testing hierarchy or adjustment of significance thresholds, depend on the trial's statistical plan. The registry record does not report a multiplicity strategy, so it is not possible to determine how the secondary outcomes were handled or whether their analyses were adjusted.

The record reports that the study was randomized and parallel-group, but it does not specify the analysis population used for the sponsor's logistic regression. It does not report whether the primary analysis followed an intention-to-treat approach, how protocol deviations were handled, or which participants were included in the model. The posted endpoint counts give the numbers of participants and events in each arm, but they do not describe missing outcome status or exclusions.

Missing data can affect estimates when outcome status is unavailable, and the appropriate method depends on how much data are missing and why. Neither the amount nor the handling of missing data is reported in the registry record. The record also does not report interim analyses, stopping rules, or further details of the analysis plan. These omissions limit assessment of the full analysis process; they do not, by themselves, show that the analysis was inappropriate.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: hypotension (10.3%), multi-organ failure (8.2%), sepsis (5.9%), septic shock (5.5%), atrial fibrillation (1.6%).

The serious adverse-event summary lists 287 affected participants among 563 at risk in the intensive group and 280 among 561 at risk in the less-intensive group. These are counts of participants with serious adverse events, not counts of distinct event episodes. A participant can potentially experience more than one event, and the registry summary does not clarify how repeat events were handled in these counts.

The record also lists other adverse events as 0 among 563 participants in the intensive group and 0 among 561 in the less-intensive group. The registry summary's categories should be read as the reported adverse-event fields; no further event definitions or collection details are reported. The listed leading serious adverse-event terms include Hypotension at 10.3%, Multi-organ failure at 8.2%, Sepsis at 5.9%, Septic shock at 5.5%, Atrial fibrillation at 1.6%, and Myocardial infarction at 1.6%. These terms are not accompanied by arm-specific percentages in the posted summary.

Deaths are not reported in the adverse-event record. The primary mortality endpoint is reported separately. Serious adverse-event counts describe events recorded during the trial; they do not alone establish that an event was caused by the assigned strategy. The registry record does not report further definitions of seriousness, attribution procedures, or timing for these events.

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

The randomized comparison addresses whether the intensive renal replacement therapy strategy differed from the less-intensive strategy in all-cause mortality by day 60. The posted counts were 302 deaths among 563 participants in the intensive group and 289 among 561 participants in the less-intensive group. The unadjusted risk-difference estimate is -0.021 for less-intensive relative to intensive therapy, and its 95% confidence interval ranges from -0.080 to 0.037. The sponsor's logistic-regression analysis reports an odds ratio of 1.09, with a 95% confidence interval from 0.86 to 1.40.

Both analyses leave uncertainty about the comparison. The recalculated interval includes zero, and the sponsor's odds-ratio interval includes 1, the respective values associated with no difference. The p-values are 0.475 for the recalculated risk difference and 0.47 for the sponsor analysis. These results do not establish a clear difference in the primary endpoint. They also do not establish that the strategies are equivalent or that any difference is absent.

The interpretation applies to the endpoint and follow-up period recorded: all-cause mortality by day 60. It does not answer whether the strategies differ on outcomes for which no results are posted, such as the secondary outcomes named in the brief summary. Nor does the endpoint estimate provide information about the timing of deaths, the cause of individual deaths, or longer-term effects beyond the stated period.

The trial summary described an anticipated reduction in mortality from 55% in the conventional arm to 45% in the intensive arm. That was the stated primary hypothesis, not the observed finding. The posted counts and analyses should be interpreted on their own terms, with their statistical uncertainty. Nothing in these results should be read as individualized medical guidance or as a conclusion about the choice of therapy for a particular patient.

17. Why This Trial Matters Statistically

This study illustrates how a randomized comparison can produce an estimate that is relatively close to no difference while still leaving a range of plausible effects. The primary outcome is straightforward to describe as a count of participants who died by day 60, but the interpretation depends on both the event counts and their uncertainty. Looking at an estimate without its interval can overstate how firmly the data determine the size or direction of a group difference.

It also shows why the effect measure matters. The recalculated risk difference expresses an absolute contrast between group risks, while the sponsor's logistic-regression result is an odds ratio. Each is a valid type of summary for a binary outcome, but the estimates are not directly interchangeable. Readers need to identify which measure is being reported and the group ordering before drawing a directional interpretation.

The record contrasts the stated hypothesis with the posted outcome data. The summary describes a hoped-for reduction from 55% to 45%, whereas the observed counts lead to an uncertain estimated comparison. A planned hypothesis is not evidence that the anticipated effect occurred. Likewise, a result that does not establish a difference should not be mistaken for proof that the groups are the same.

Finally, the sample-size illustrations demonstrate how planning needs depend on the target effect and desired power. Planning around smaller effects requires more participants under the stated assumptions. These are planning calculations rather than a reconstruction of the trial's original design, which is not reported in the registry record. Together, these points make the record useful for distinguishing trial hypotheses, observed estimates, precision, and planning assumptions.

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 registry record gives aggregate counts for the primary outcome, but does not provide participant-level data. The recalculated comparison is therefore unadjusted and cannot examine the influence of baseline characteristics or support alternative adjusted models. The sponsor reports logistic regression, but the covariates, model specification, and analysis population are not reported, limiting independent assessment of that analysis.

The record does not report missing outcome data or how missingness was handled. It also does not report the allocation method in detail, protocol deviations, the analysis population definition, or an interim monitoring plan. These details matter for evaluating the analysis process, but their absence from the registry record does not demonstrate a specific flaw.

Although the brief summary names secondary outcomes, their results are not posted. Interpretation is consequently restricted to the 60-day all-cause mortality endpoint and the adverse-event information reported. The summary also refers to a planned recruitment target of 1164, while the reported enrollment is 1124; the registry record does not explain this difference. No reason for the difference should be inferred from the posted figures alone.

The posted serious adverse-event terms are not broken down by treatment group in the summary, and event definitions, attribution, and timing are not reported. The adverse-event counts therefore offer limited detail for comparing the groups. Finally, the findings address the trial's described population and day-60 endpoint; the registry record alone does not establish how results apply to populations or outcomes not described there.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Acute Renal Failure Trial Network (ATN) Study — NCT00076219.
• Registry record last updated 2013-08-23; status last verified 2013-08.
• Results first posted 2013-08-16.
• 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

The Acute Renal Failure Trial Network Study was a completed phase 3 randomized parallel-group trial sponsored by the US Department of Veterans Affairs. It enrolled 1124 participants and compared intensive with less-intensive renal replacement therapy. Masking is listed as none.

The primary endpoint was all-cause mortality by day 60. The registry reports 302 deaths among 563 participants in the intensive group and 289 among 561 in the less-intensive group. The sponsor's logistic-regression analysis reports an odds ratio of 1.09, with a 95% confidence interval from 0.86 to 1.40 and p = 0.47. The unadjusted recalculation reports a risk difference of -0.021, with a 95% confidence interval from -0.080 to 0.037 and p = 0.475.

The estimates are uncertain and do not establish a clear difference between strategies in day-60 mortality. The registry record does not post the secondary outcomes named in the trial summary or report several analysis details, including missing-data handling and the sponsor model specification.