Efficacy and Safety Study to Evaluate Vadadustat for the Maintenance Treatment of Anemia in Participants With Dialysis-dependent Chronic Kidney Disease (DD-CKD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study to Evaluate Vadadustat for the Maintenance Treatment of Anemia in Participants With Dialysis-dependent Chronic Kidney Disease (DD-CKD) (NCT02892149), a randomized phase 3 study. The primary outcome is Change From Baseline in Hemoglobin (Hb) to the Average Over the Primary Efficacy Period (Weeks 24 to 36).

2. Clinical Question

3. Trial Design

The registry record describes NCT02892149 as a Phase 3, randomized, open-label, active-controlled, parallel-group study. It evaluated oral vadadustat for maintenance treatment of anemia in participants with dialysis-dependent chronic kidney disease. Darbepoetin alfa was the active comparator. The record identifies the trial as multicenter and reports that it is completed.

The posted overall enrollment is 3554. For the primary outcome, the randomized population is defined as all participants randomized, with analyses based on randomized treatment. The outcome summaries report 1777 participants in each treatment group. Those group figures describe the posted primary outcome analysis; the registry record does not provide a fuller account of participant flow, withdrawals, or the number contributing data at each assessment.

The primary completion date is 2020-01-16, and the reported study start is 2016-08. These dates describe the registry record and do not, by themselves, explain the timing of individual assessments or follow-up. The primary efficacy period for the hemoglobin endpoint was Weeks 24 to 36, with a later secondary efficacy period at Weeks 40 to 52.

Because the study was open-label, participants and study personnel were not masked to treatment assignment as described in the record. Random allocation supports a comparative design, while the active control makes the question a comparison against an established trial treatment rather than against no treatment. The registry record does not report the randomization procedure, allocation ratio in protocol terms, original sample-size justification, or planned interim analyses. These details should not be inferred from the observed enrollment or posted results.

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: A total of 4944 participants were screened for entry into the study. Of these, 3554 participants were enrolled and randomized in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomized Population: All participants randomized. Analyses of this population were based on the randomized treatment.

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 Change From Baseline in Hemoglobin (Hb) to the Average Over the Primary Efficacy Period (Weeks 24 to 36), measured over Baseline; Weeks 24 to 36.

The primary endpoint is change from baseline in hemoglobin (Hb), measured as the average over the Primary Efficacy Period, Weeks 24 to 36, in grams per deciliter. The baseline average was calculated from Hb values at the screening visit closest to randomization and at the randomization visit. The period average was calculated from Hb values over Weeks 24 to 36.

This endpoint summarizes hemoglobin maintenance across a specified time window rather than relying on a single measurement. Averages can reflect the pattern of repeated measurements during that period, although the registry record does not give the measurement schedule or further details about which observations were available for each participant.

Hemoglobin is the clinical measure selected for the primary efficacy comparison in this anemia study. The sponsor’s registered analysis used an analysis of covariance (ANCOVA) model with multiple imputation for missing data and adjusted for baseline hemoglobin category, geographic region, and New York Heart Association congestive heart failure class. The baseline categories were <10.0 versus ≥10.0 g/dL; the listed regions were United States, European Union, and Rest of World; and the listed heart failure classes were Class 0 or I versus Class II or III.

The endpoint’s clinical importance does not establish by itself whether the treatments meet the trial’s intended non-inferiority criterion. That conclusion depends on the prespecified analysis and margin, and the margin is not reported in the registry record.

7. Results Posted in the Registry

• Darbepoetin Alfa: mean 0.36 versus 0.19 on control; difference 0.17 (95% CI 0.08 to 0.26), standardized effect d = 0.13; z-test p = <0.001.

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.

Change From Baseline in Hb to the Average Over the Secondary Efficacy Period (Weeks 40 to 52)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Darbepoetin Alfa: mean 0.41 versus 0.23 on control; difference 0.18 (95% CI 0.09 to 0.27), standardized effect d = 0.13; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Darbepoetin Alfa than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Median Time to First MACE Plus Hospitalization for Heart Failure or Thromboembolic Event Excluding Vascular Access Thrombosis

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Vadadustat vs Darbepoetin Alfa: hazard ratio 0.96 (95% CI 0.83–1.10), reported p = 0.372 (as reported in the registry).
  • Vadadustat vs Darbepoetin Alfa: hazard ratio 0.96 (95% CI 0.84–1.10), reported p = =0.4096 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Vadadustat vs Darbepoetin Alfa and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Vadadustat vs Darbepoetin Alfa and the control. The interval gives the range of effects that remain compatible with the data.

Median Time to First Cardiovascular MACE

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Gray's test); it was not recalculated.
• Result:
  • Vadadustat vs Darbepoetin Alfa: hazard ratio 0.94 (95% CI 0.78–1.13), reported p = 0.388 (as reported in the registry).
  • Vadadustat vs Darbepoetin Alfa: hazard ratio 0.95 (95% CI 0.80–1.14), reported p = =0.5007 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Vadadustat vs Darbepoetin Alfa and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Vadadustat vs Darbepoetin Alfa and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning later-period hemoglobin change and time-to-event cardiovascular or related events. The posted estimates therefore extend the primary question in two different ways: they examine whether the hemoglobin pattern continues during a later efficacy period, and they describe selected event outcomes during follow-up. These outcomes are related to the study’s broader evaluation but do not measure the same quantity as the primary hemoglobin endpoint.

The overall pattern should be read as a set of estimates with uncertainty, not as a single unified verdict. The later hemoglobin comparison is directionally similar to the primary comparison in the posted arm means. The time-to-event results have confidence intervals spanning the no-relative-difference value. Differences in outcome definition, event frequency, analysis method, and follow-up mean that these findings cannot simply be pooled or treated as direct replications of the primary result.

The registry names additional mortality-related secondary outcomes, including cardiovascular death and all-cause mortality. The detailed secondary statistics summarized for this analysis are not available for every named outcome; further details are not reported in the registry record. Accordingly, conclusions should be limited to outcomes with posted estimates.

Secondary outcomes commonly involve multiple comparisons. In general, examining many outcomes increases the possibility of finding apparently notable results by chance, especially when no adjustment is made. The registry record does not report a multiplicity adjustment plan for these secondary analyses. Their results are therefore useful for context and further questions, but carry less confirmatory weight than a prespecified primary analysis with a clearly stated decision rule. No single secondary estimate should override the limitations of the primary non-inferiority interpretation.

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

• Change From Baseline in Hb to the Average Over the Secondary Efficacy Period (Weeks 40 to 52)
• Median Time to First MACE Plus Hospitalization for Heart Failure or Thromboembolic Event Excluding Vascular Access Thrombosis
• Median Time to First Cardiovascular MACE
• Median Time to First Cardiovascular Death
• Median Time to First All-cause Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a change in hemoglobin measured in g/dL. The posted arm summaries are least-squares means with standard errors. A least-squares mean is a model-based mean adjusted for the covariates included in the analysis, rather than necessarily the raw arithmetic average among participants with observed measurements. The registry describes the adjusted primary analysis, although the posted outcome summary does not reproduce all model details.

What does ANCOVA contribute?

Analysis of covariance (ANCOVA) compares outcome means while accounting for selected baseline or design characteristics. In general, adjustment can improve precision when those characteristics are associated with the outcome, and it can address imbalances in the variables included in the model. It does not automatically correct for unmeasured differences or replace randomization. The registry lists baseline Hb category, geographic region, and NYHA CHF class as covariates. It does not report every modeling choice, such as the full specification of terms or diagnostic checks, so those should not be assumed.

How does multiple imputation fit in?

The primary model is described as using multiple imputation for missing data. In general, multiple imputation creates multiple plausible completed datasets under an assumed model for missingness and combines the resulting estimates to reflect uncertainty from both sampling and imputation. Its validity depends on the imputation model and assumptions about why values are missing. The registry record does not report those details, the amount or pattern of missing Hb data, or sensitivity analyses addressing departures from the imputation assumptions. The method’s presence is informative, but it does not alone show how robust the result is to missing-data assumptions.

What does the unadjusted recalculation represent?

The recalculated mean difference uses the posted arm-level means and standard errors to make a simple comparison. It is explicitly unadjusted, while the sponsor’s primary result is a least-squares mean difference from the registered non-inferiority analysis. The recalculation is useful as a check on the scale and direction of the contrast and to illustrate uncertainty from posted summary statistics. It does not reproduce the ANCOVA with multiple imputation, and its p-value is not the sponsor’s non-inferiority test. The record reports no discrepancy flag for the primary result; nevertheless, the sponsor’s reported analysis is the relevant result for the trial’s stated analysis.

How should the time-to-event methods be read?

The secondary time-to-event outcomes report median times and hazard ratios. A median time is the point by which half of the event-time distribution has occurred under the analysis definition; it is not a mean and does not describe every participant’s event time. A hazard ratio compares event rates over follow-up under the model or test used. In general, a hazard ratio near 1 indicates similar estimated relative event rates, while its confidence interval communicates the range of values compatible with the data and analysis assumptions.

The composite time-to-first outcome was analyzed with a Log Rank method in the registry’s reported analysis. The cardiovascular MACE result was analyzed using Gray’s test. These methods address time-to-event comparisons, but the registry record does not provide enough detail to reconstruct the handling of censoring, competing events, or all model assumptions. The methods should therefore be described as reported, not expanded into unreported protocol claims.

Why do confidence intervals and p-values differ in purpose?

A confidence interval expresses uncertainty around an estimate on the outcome’s scale. A p-value addresses compatibility with a specified null hypothesis under the analysis assumptions. Neither is a direct measure of clinical importance. For non-inferiority, interpretation additionally requires a justified margin and the appropriate analysis framework; the margin is not reported in the registry record. For secondary outcomes, multiple comparisons can also affect how much weight to place on isolated p-values. The registry record does not report a multiplicity adjustment plan.

General statistical context is useful, but trial-specific claims must remain tied to the registry. In particular, the record does not report the original sample-size justification, interim analysis plan, full missing-data assumptions, or all details needed to assess model diagnostics. Those omissions limit independent reconstruction, even when summary estimates and named methods are available.

11. Confidence Intervals and Precision

The primary recalculated mean difference is 0.17 g/dL, with a 95% confidence interval from 0.081 to 0.259. This interval describes uncertainty around the unadjusted difference in the direction darbepoetin alfa relative to vadadustat. It does not mean that 95% of participants had differences within these limits. Under the assumptions of the calculation, it indicates a range of values compatible with the observed summaries and method.

The sponsor’s reported least-squares mean difference is -0.17, with a 95% confidence interval from -0.23 to -0.10. Its contrast direction is opposite to the recalculation’s, and the sponsor’s result comes from the registered analysis rather than the simple summary-statistic recalculation. The confidence intervals should not be treated as the same analysis merely because their point estimates have the same magnitude after reversing direction.

For the secondary time-to-event outcomes, the reported hazard-ratio confidence intervals extend across 1. In general, that means the data are compatible with values on either side of the no-relative-difference reference under the stated analysis. The intervals also show that estimates are not exact; possible effects span a range. Their width should be considered alongside the event definitions, analysis methods, and follow-up.

Precision is not the same as clinical relevance. A narrow interval can still leave the key clinical question unanswered if a decision margin is missing, and a point estimate alone does not show the range of uncertainty. The registry record does not report a non-inferiority margin, so the primary confidence interval cannot be judged against that threshold from the record alone. The standard errors and intervals quantify statistical uncertainty, not the probability that a treatment is beneficial or acceptable.

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 illustrations based on the observed effect, not the trial’s original design calculations. For continuous outcomes, the figures are participants per arm. For time-to-event outcomes, they are total events, not participants. Read each row as a planning scenario for detecting the stated fraction of the observed effect, with separate columns for 80% and 90% power. In plain language, a power column gives the number of participants per arm, or total events for time-to-event outcomes, that the stated planning assumptions would require for the chosen chance of detecting that effect if it were present.

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. For time-to-event calculations, the method is Schoenfeld and the output is total events. The registry record does not report the trial’s original sample-size assumptions or justification, so these illustrations should not be read as a reconstruction of the study’s planning.

Smaller effects require more information to detect under these assumptions. That is why planning for 75% or 50% of the observed effect calls for larger sample sizes or event counts than planning for the full observed effect. The 90% power target also requires more information than the 80% target for the same scenario. These are prospective planning concepts applied to observed estimates; they do not show that the completed trial had a particular probability of success. This is not observed power.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.170; pooled standard deviation σ = 1.349.
2. n = 2 × (1.96 + 0.842)² × 1.349² / 0.170² = 988.4, rounded up to 989 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.17                      # observed difference in means
sigma <- 1.34894329013491                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2892149)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 989 (80% power), 1,324 (90% power)
 75% of observed effect: n per arm = 1,758 (80% power), 2,353 (90% power)
 50% of observed effect: n per arm = 3,954 (80% power), 5,293 (90% power)
power.t.test: 989.3 
Simulated power at n = 989 per arm: 0.804 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a least-squares mean difference of -0.17, with a 95% confidence interval from -0.23 to -0.10, classified as non-inferiority. That result reflects the sponsor’s stated analysis framework, including ANCOVA and multiple imputation for missing data. The registry record does not provide the non-inferiority margin, so the reported interval cannot be checked against the criterion required to interpret non-inferiority.

The simple recalculation from the posted arm summaries gives a mean difference of 0.17 in the opposite contrast direction, with a 95% confidence interval from 0.081 to 0.259 and p < 0.001. It is an unadjusted comparison, not a reproduction of the sponsor’s model. Reversing the direction of a contrast changes the sign, so the opposite signs do not by themselves indicate conflicting results. The record indicates no discrepancy for this outcome.

The recalculation can help readers understand the scale of the observed difference, but it does not replace the sponsor’s analysis for the registered non-inferiority question. The registry record does not give enough detail to independently reproduce the sponsor’s model or evaluate all its assumptions. Interpretation should therefore distinguish clearly between the sponsor-reported non-inferiority analysis and the unadjusted recalculation.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome analysis is described as ANCOVA with multiple imputation and adjustment for baseline hemoglobin category, geographic region, and NYHA CHF class. The analysis population is the randomized population: all participants randomized, analyzed according to randomized treatment. These details identify important parts of the analysis approach, but they do not amount to a complete statistical analysis plan.

The registry record does not report whether or how multiplicity was controlled across secondary outcomes, multiple time points, or the multiple reported analyses for some time-to-event outcomes. Without that information, isolated secondary p-values should be interpreted cautiously. In general, testing multiple hypotheses without an adjustment can raise the chance of at least one apparently unusual result even when no corresponding effect exists. This general concern does not establish that a particular result is false; it limits how strongly such results can be treated as confirmatory.

Multiple imputation is reported for the primary outcome, but the registry record does not report the number or pattern of missing Hb values, the imputation model, the assumptions about missingness, or sensitivity analyses. These details matter because conclusions can depend on assumptions about unobserved outcomes. The record also does not report a full account of missing-data handling for the secondary outcomes.

The original sample-size justification, interim analysis plan, and the non-inferiority margin are not reported in the registry record. These omissions prevent a full assessment of the planned power rationale, any potential impact of repeated examination of accumulating data, and whether the primary interval meets the intended non-inferiority criterion. The reported randomized population is useful context, but participant flow and outcome-specific availability are not fully described in the registry record for this analysis. These reporting limits should be kept distinct from the estimates that are posted.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (7.9%), fluid overload (5.5%), sepsis (5.0%), acute myocardial infarction (4.6%), hyperkalaemia (4.3%).

The registry reports serious adverse event counts and other adverse event counts among participants at risk in each treatment group, as well as deaths. These are counts as recorded, not estimates of treatment effects. The at-risk figures differ between the safety groups, and the record does not provide a comparative statistical analysis of these counts in the information.

The most frequently listed serious adverse event terms include pneumonia, fluid overload, sepsis, acute myocardial infarction, hyperkalaemia, and cardiac arrest, with percentages recorded for those terms. The registry excerpt does not specify a treatment-group breakdown for that list, so those percentages should not be assigned to either group. Nor do event counts alone establish that an event was caused by treatment. Serious adverse events, other adverse events, and deaths are distinct reporting categories.

To compare safety formally, readers would need consistent definitions, follow-up context, exposure information, and appropriate comparative analyses. The registry record does not report all of those details in the information summarized for this analysis. The posted figures describe reported events; they do not by themselves establish a causal safety difference or provide medical advice.

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

The primary result describes average hemoglobin change during Weeks 24 to 36 in a randomized, active-controlled study of participants with DD-CKD. The posted least-squares means and sponsor analysis provide a statistical comparison between vadadustat and darbepoetin alfa. The simple recalculation adds an unadjusted estimate and confidence interval based on posted summary statistics. These are statistical descriptions of the trial data, not a complete account of individual response.

The sponsor classifies its primary result as a non-inferiority analysis. However, the non-inferiority margin is not reported in the registry record. A non-inferiority conclusion depends on comparing the appropriate confidence bound with a prespecified margin, not merely on the direction or p-value of a difference. The posted record therefore does not allow the margin-based decision to be independently assessed in the registry record.

The results do not establish that the treatments are identical. A failure to distinguish treatments on a particular outcome would not prove equivalence, and statistical evidence of a mean difference does not by itself establish clinical importance. Likewise, the secondary time-to-event estimates concern different outcomes and should not be used to make broad claims beyond their definitions and uncertainty.

The study was randomized but open-label. Randomization is a design strength for balancing groups on average, while lack of masking can matter for outcomes influenced by awareness of treatment. The primary outcome is a laboratory measure, but the record does not report enough information to assess every potential source of bias or missingness. The appropriate interpretation is therefore bounded: the registry provides estimates for specified outcomes in this trial, with important protocol and analysis details not reported. It does not support medical advice or a universal conclusion about all patients or settings.

18. Why This Trial Matters Statistically

This trial illustrates why a registry result needs to be read through the lens of its estimand and analysis design. The primary endpoint is a continuous hemoglobin measure averaged across a defined period, while the sponsor frames the comparison as non-inferiority. Those are not interchangeable concepts: the endpoint describes what was measured, whereas non-inferiority is a decision framework that requires a prespecified margin.

It also shows why contrast direction matters. The sponsor reports a negative least-squares mean difference, while an unadjusted recalculation expresses the comparison in the opposite direction and is positive. Direction changes the sign, not the underlying contrast. Distinguishing the adjusted sponsor analysis from a summary-statistic recalculation helps prevent readers from mistaking differences in method or coding for conflicting findings.

Uncertainty is central to interpretation. Confidence intervals show a range of estimates compatible with the data under stated methods, while p-values address a particular null hypothesis. Neither alone answers whether a difference is clinically acceptable. This is especially important when the non-inferiority margin is not reported and when secondary outcomes involve multiple comparisons.

Finally, the record highlights the value of transparent reporting of missing-data assumptions, multiplicity plans, sample-size rationale, and analysis details. Randomization and a clearly described primary outcome provide a useful basis for comparison, but incomplete reporting limits independent evaluation. Statistical interpretation should therefore be precise about what is observed, what is modeled, and what remains unreported.

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.

Several limitations specific to this trial follow from the registry information. The primary analysis is described as adjusted ANCOVA with multiple imputation, but the imputation model, missingness patterns, and sensitivity analyses are not reported in the registry record. The extent to which the result depends on assumptions about missing outcomes therefore cannot be evaluated from the posted details.

The sponsor labels the primary analysis non-inferiority, but the margin and its clinical justification are not reported. Without them, the margin-based interpretation cannot be independently checked. The registry record also does not report the complete original sample-size justification, interim analysis plan, or full statistical analysis plan.

The open-label design means treatment assignment was not masked. This can be relevant to care, reporting, and outcome assessment, although the primary endpoint is a measured laboratory value. The record does not provide enough detail to determine the extent of any resulting influence. The randomized population definition is stated, but participant flow and outcome-specific missingness are not fully described in the information.

For secondary outcomes, the registry lists more outcomes than have detailed estimates in the available summary, and it does not report a multiplicity adjustment plan. Some time-to-event outcomes have multiple reported analyses. Definitions and methods differ across outcomes, and the registry does not give enough detail to reconstruct all handling of censoring or competing events. Safety counts are descriptive and do not constitute a comparative causal analysis. These limitations do not invalidate the posted estimates, but they constrain the strength and scope of conclusions drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety Study to Evaluate Vadadustat for the Maintenance Treatment of Anemia in Participants With Dialysis-dependent Chronic Kidney Disease (DD-CKD) — NCT02892149.
• Registry record last updated 2022-06-28; status last verified 2022-06.
• Results first posted 2022-06-28.
• 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

NCT02892149 is a completed, Phase 3, randomized, open-label, active-controlled, parallel study of vadadustat and darbepoetin alfa for maintenance treatment of anemia in participants with dialysis-dependent chronic kidney disease. The primary endpoint was change from baseline in hemoglobin averaged over Weeks 24 to 36. The registry reports a sponsor non-inferiority analysis and supports a simple unadjusted recalculation from the posted arm summaries.

The primary analysis used ANCOVA with multiple imputation and listed baseline Hb category, geographic region, and NYHA CHF class as covariates. The registry also reports selected secondary hemoglobin and time-to-event results and adverse-event counts. The non-inferiority margin, original sample-size justification, full missing-data assumptions, and multiplicity plan are not reported in the registry record, limiting independent evaluation of several aspects of the trial’s interpretation.