Efficacy and Safety Study to Evaluate Vadadustat for the Maintenance Treatment of Anemia in Participants With Non-dialysis-dependent Chronic Kidney Disease (NDD-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 Non-dialysis-dependent Chronic Kidney Disease (NDD-CKD) (NCT02680574), 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

In statistical terms, the primary question is whether the average Hb change during the primary efficacy period differed between the randomized treatment groups, under the specified adjusted analysis. The registry also posts an analysis of the difference between groups with a confidence interval. A confidence interval describes uncertainty around an estimate; interpreting it against a non-inferiority margin requires knowing that margin and the prespecified direction of comparison. Those details are not reported in the registry record.

3. Trial Design

This was a Phase 3, randomized, open-label, active-controlled, parallel-group study of vadadustat and darbepoetin alfa for maintenance treatment of anemia in participants with NDD-CKD. The brief description identifies it as multicenter. The registry lists enrollment as 1725 and status as completed. The recorded start is 2016-02, and the primary completion date is 2020-06-18. The sponsor is Akebia Therapeutics.

Randomization assigns participants to treatment groups by chance. In general, this can help balance measured and unmeasured characteristics between groups, although it does not guarantee exact balance. The primary endpoint population is described as all randomized participants, with analyses based on randomized treatment. That is a randomized-treatment analysis description; the registry does not provide further population definitions or a participant-flow account in the registry record reported for these results.

Open-label means treatment assignment was not masked. This can matter for care decisions, additional treatment, and reporting of subjective outcomes. Hemoglobin is a laboratory measure, but the open-label design can still be relevant to broader study conduct and other outcomes. The registry record does not describe procedures intended to limit these influences.

The primary efficacy period was Weeks 24 to 36, with baseline defined using the average of hemoglobin values from the screening visit closest to randomization and the randomization visit. The secondary hemoglobin period was Weeks 40 to 52. Several cardiovascular and other time-to-event outcomes were also listed, with a timeframe of up to Week 208. The record does not give the protocol’s full schedule of assessments or a detailed rationale for the selected periods.

The study’s own sample-size rationale, allocation ratio beyond the fact of randomization, stratification procedures, interim analyses, and original statistical plan are not reported in the registry record. Those omissions limit what can be inferred about the planning choices and analysis decisions made before results were available.

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 2961 participants were screened for entry into the study. Of these, 1725 participants were enrolled and randomized into 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 was change from baseline in hemoglobin (Hb) to the average over the primary efficacy period, Weeks 24 to 36, measured in grams per deciliter. The baseline average used Hb values from the screening visit closest to randomization and the randomization visit. The endpoint-period average used Hb values over Weeks 24 to 36. The registry reports least-squares means, which are model-based group estimates adjusted for the covariates named in the analysis description.

Hemoglobin is a continuous measure, so the primary result is expressed as an average change rather than as a count of participants who crossed a threshold. Comparing average changes can describe how the groups differed on this measure over a defined period. The registry reports a least-squares mean change of 0.41 for vadadustat and 0.42 for darbepoetin alfa. Their posted standard errors are 0.036 and 0.037, respectively. These are standard errors, which quantify uncertainty in estimated means; they are not measures of the spread of individual Hb values.

In general, a maintenance endpoint asks whether the measured level is sustained over a specified period rather than focusing on a single measurement. Averaging Hb across the efficacy window can reduce the influence of any one reading, although it does not remove all measurement variability or uncertainty. The endpoint is clinically relevant to the stated aim of anemia maintenance, but the registry results alone do not establish the broader benefits or risks of either treatment.

The sponsor’s posted analysis is classified as non-inferiority, but the non-inferiority margin and full decision rule are not reported in the registry record. Consequently, the numerical estimate and its interval can be described, but the non-inferiority conclusion cannot be independently assessed from the listed information alone.

7. Results Posted in the Registry

• Darbepoetin Alfa: mean 0.42 versus 0.41 on control; difference 0.01 (95% CI -0.09 to 0.11), standardized effect d = 0.01; z-test p = 0.846.

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 0.44 versus 0.43 on control; difference 0.01 (95% CI -0.11 to 0.13), standardized effect d = 0.01; z-test p = 0.872.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Darbepoetin Alfa and the control. The interval gives the range of effects that remain compatible with the data.

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 1.04 (95% CI 0.85–1.27), reported p = =0.7770 (as reported in the registry).
  • Vadadustat vs Darbepoetin Alfa: hazard ratio 1.11 (95% CI 0.97–1.27), reported p = =0.2305 (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 1.11 (95% CI 0.82–1.50), reported p = =0.5509 (as reported in the registry).
  • Vadadustat vs Darbepoetin Alfa: hazard ratio 1.16 (95% CI 0.95–1.42), reported p = =0.2531 (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 secondary results extend the primary Hb comparison to a later efficacy period and to cardiovascular and other time-to-event outcomes. Across the posted results, there is no clear pattern of large separation between the treatment groups in the displayed estimates, but that broad observation should not be treated as proof that the treatments have the same effects. The secondary Hb estimates are close to the primary estimates, while time-to-event estimates have their own endpoint definitions, methods, and levels of precision.

These outcomes complement the primary result by addressing a later Hb period and events beyond the laboratory endpoint. They do not replace the primary analysis or resolve the missing information needed to judge its non-inferiority criterion. The registry reports more than one analysis for some time-to-event outcomes, without explaining the distinction between the estimates. That limits a unified interpretation of the secondary evidence.

In general, when many outcomes or analyses are examined, the chance of at least one apparently notable result can increase if no adjustment is made for multiple comparisons. The registry record lists multiple secondary outcomes and analyses, but does not report a multiplicity adjustment or a hierarchy specifying which secondary analyses were confirmatory. Consequently, secondary p-values and confidence intervals should be read as supportive or exploratory evidence unless additional prespecified analysis details are available. Their statistical weight is lower than that of the designated primary endpoint, and they should not be selectively emphasized.

Overall, the secondary endpoints provide additional context rather than a separate basis for a definitive treatment conclusion. The posted results are constrained by incomplete reporting of analysis distinctions, multiplicity handling, and time-to-event methods. Those limitations warrant caution when comparing endpoints or treating one secondary estimate as decisive.

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 analysis is described as an analysis of covariance (ANCOVA) with multiple imputation for missing data. It used baseline hemoglobin concentration, geographic region, and New York Heart Association congestive heart failure class as covariates. In general, ANCOVA estimates group differences while adjusting for specified characteristics. Adjustment can account for chance imbalances in those measured characteristics and can improve precision when the covariates are informative. It does not adjust for factors omitted from the model, and it does not establish that the model’s assumptions were satisfied.

What does the adjusted mean represent?

The registry labels the primary group estimates as least-squares means. In general, a least-squares mean is a model-based estimate that accounts for covariates in the analysis, rather than a simple arithmetic average of every observed value. The registry reports the two group estimates as 0.41 and 0.42 g/dL. The sponsor’s reported contrast is a least-squares mean difference of -0.01. That contrast is the result to use when describing the sponsor’s adjusted primary analysis. The registry does not provide further model coefficients, diagnostics, or details sufficient to reconstruct the model.

Why use multiple imputation?

Multiple imputation is a general approach to handling missing observations. It creates multiple plausible completed datasets using a statistical model, analyzes each dataset, and combines the results so that uncertainty due to missingness is reflected in the final estimate. Its validity depends on assumptions about how data became missing and on the imputation model. The registry says that multiple imputation was used, but it does not report the amount or pattern of missing data, the imputation model, or sensitivity analyses addressing departures from its assumptions. The method’s presence therefore does not, by itself, establish that missing-data bias was eliminated.

What do standard errors describe?

The arm-level Hb estimates are accompanied by standard errors. In general, a standard error describes uncertainty in an estimated quantity across repeated samples under a statistical model. It is not the same as a standard deviation, which describes variability among individual observations. The posted standard errors are 0.036 for vadadustat and 0.037 for darbepoetin alfa for the primary endpoint. The registry does not post arm-level confidence limits for these estimates in the registry record.

How should the unadjusted calculation be understood?

The re-calculated primary comparison uses posted group summaries to make a simple, unadjusted comparison. It gives an estimated difference of 0.01, an approximate confidence interval from -0.091 to 0.111, and p = 0.846. Because the group summaries are least-squares means and their standard errors, and because the recalculated standard deviation is approximate, this is not a reconstruction of the sponsor’s ANCOVA with imputation. In general, an unadjusted test and a covariate-adjusted analysis can differ because they use different information and modeling choices. The registry record does not flag a discrepancy, but the sponsor-reported analysis remains the trial’s posted adjusted result.

What does a confidence interval say?

In general, a confidence interval expresses the precision of an estimate under a specified method. A wider interval indicates less precision than a narrower interval on the same scale. A 95% confidence interval is often described through the long-run behavior of the method: across repeated samples under its assumptions, intervals formed in that way would cover the true parameter in 95% of cases. It is not a statement that there is a 95% probability that this particular fixed parameter lies inside the calculated interval. Interpretation also depends on the endpoint definition and model used.

How do time-to-event analyses differ?

The registry reports medians, hazard ratios, confidence intervals, p-values, and methods for selected time-to-event outcomes. In general, a median time is the time by which half of the relevant observed event-time distribution has occurred, subject to the study’s analysis and censoring. A hazard ratio compares event rates over time between groups under the model or method used; it is not a direct comparison of median times. A hazard ratio of 1 represents no relative difference on the hazard-ratio scale. The registry lists Log Rank or Gray’s Test for these analyses, but it does not report enough detail to reconstruct the time-to-event models, censoring rules, or the reason for the multiple reported estimates.

Gray’s Test is a general method used when competing events may affect the occurrence of the event of interest. Competing events matter because they can prevent the event under study from occurring. Whether and how that issue was handled for each listed outcome cannot be fully assessed from the registry record. The posted descriptions identify the method but do not give the detailed analysis specification.

What does a p-value contribute?

In general, a p-value measures how incompatible the observed data are with a specified null hypothesis, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The unadjusted primary p-value is 0.846; the sponsor’s reported primary analysis does not list a p-value. For non-inferiority, the key question is whether the confidence interval satisfies a prespecified margin in the required direction, not simply whether a conventional test for difference is statistically significant. That margin and testing procedure are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor-reported primary least-squares mean difference is -0.01, with a 95% confidence interval from -0.09 to 0.07. The interval crosses zero, which means the posted data are compatible with a small difference in either direction under the sponsor’s analysis. It also shows that the estimate is not precise enough to identify a single exact difference. Whether the interval is sufficiently narrow for a non-inferiority conclusion cannot be determined without the non-inferiority margin, which is not reported in the registry record.

The unadjusted re-calculation gives a mean difference of 0.01 and an approximate interval from -0.091 to 0.111. This interval is not the sponsor’s adjusted confidence interval. It is derived from posted summary statistics and relies on an approximate pooled standard deviation, so it should be treated as a supplementary, unadjusted estimate rather than the primary inferential result.

For the secondary Hb period, the sponsor-reported difference is -0.00, with a 95% confidence interval from -0.10 to 0.09. The interval again includes zero. Its width describes uncertainty around the estimated contrast, but it does not show whether the result meets any non-inferiority criterion. No such margin is reported.

For time-to-event endpoints, the registry reports 95% confidence intervals for hazard ratios. In general, the position and width of an interval indicate both the estimated relative event rate and the range of values compatible with the data and method. Intervals that include 1 are compatible with no relative difference on the hazard-ratio scale as well as with effects in either direction. They do not establish equivalence. The listed intervals vary in width, so the precision differs across endpoints; event counts, censoring, and analysis details also influence that precision.

Confidence intervals quantify statistical uncertainty under the analysis assumptions. They do not incorporate every possible source of uncertainty, such as incomplete reporting, model misspecification, or limitations in the design. The registry record does not report the non-inferiority margin, detailed missing-data diagnostics, or full time-to-event specifications, all of which are important to a complete assessment of precision and interpretation.

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 assumptions. The registry does not report the trial’s own sample-size justification. The stated illustration 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 set as the stated fraction of the observed effect. For continuous outcomes, the figures are participants per arm; for time-to-event outcomes, they are total events, calculated using the Schoenfeld approach.

The 80% power column describes the planning number needed for an analysis to have an 80% chance of detecting the specified effect under the illustration’s assumptions, if that effect and those assumptions were true. The 90% power column describes the corresponding planning number for a 90% chance. These are planning concepts, not guarantees about a future study: actual power and precision depend on the effect, variability, outcome frequency, missingness, and analysis.

The continuous-outcome illustrations show planning at 100%, 75%, and 50% of the observed effect. The time-to-event illustrations use the same stated fractions and express requirements as total events rather than participants per arm. Smaller effects require more participants or events to detect under the same assumptions, because they are harder to distinguish from random variation. The values are illustrations based on observed effects and are not observed power.

The original design assumptions, including the effect size used to plan the actual trial, are not reported in the registry record. The planning illustrations therefore should not be read as evidence that the completed study was designed to a particular power level, or as a substitute for the sponsor’s analysis and its prespecified decision criteria.

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 = 0.010; pooled standard deviation σ = 1.072.
2. n = 2 × (1.96 + 0.842)² × 1.072² / 0.010² = 180,417.2, rounded up to 180,418 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 <- 0.01                      # observed difference in means
sigma <- 1.07206257180455                     # 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(2680574)
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 = 180,418 (80% power), 241,528 (90% power)
 75% of observed effect: n per arm = 320,742 (80% power), 429,383 (90% power)
 50% of observed effect: n per arm = 721,669 (80% power), 966,110 (90% power)
power.t.test: 180418.2 
Simulated power at n = 180,418 per arm: 0.794 (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 sponsor’s reported primary result is a least-squares mean difference of -0.01, with a 95% confidence interval from -0.09 to 0.07, classified in the registry as a non-inferiority analysis. The registry does not report a p-value for this primary analysis. The sponsor’s adjusted result is distinct from the simple unadjusted re-calculation, which gives a mean difference of 0.01, an approximate interval from -0.091 to 0.111, and an unadjusted p-value of 0.846.

The two estimates are not contradictory merely because their point estimates have opposite signs. They come from different analyses: one is the sponsor’s reported least-squares mean contrast, while the other is a simple re-calculation from posted summaries. The sponsor analysis incorporates the specified ANCOVA and multiple imputation; the re-calculation does not reproduce those procedures. The registry record does not flag a discrepancy between the two.

The sponsor result is the appropriate primary result to quote when describing the trial’s posted analysis. However, the non-inferiority margin and the prespecified testing rule are not reported in the registry record. Without them, the reported estimate and interval cannot independently verify whether the sponsor’s non-inferiority criterion was satisfied. The unadjusted calculation offers a supplementary view of the summary data but cannot fill that reporting gap.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome is clearly identified as change from baseline in Hb averaged over Weeks 24 to 36. The registry also lists a later Hb outcome and several time-to-event outcomes, with multiple reported analyses for some of them. In general, testing many outcomes or analysis variants can increase the chance of false-positive findings if each is interpreted using an unadjusted threshold. A prespecified hierarchy or multiplicity adjustment can address this issue, but neither is described in the registry record for the posted results.

The record’s primary method includes multiple imputation for missing Hb data. It does not state how much data were missing, when they were missing, how the imputation model was specified, or whether sensitivity analyses examined alternative assumptions. In general, missing-data methods rely on assumptions about the relationship between observed and unobserved values. If those assumptions are not credible, estimates may be biased despite use of a formal imputation procedure. The registry entries are insufficient to judge this risk.

The primary population is described as all randomized participants, with analyses based on randomized treatment. This provides a useful statement of the intended analysis population, but the registry does not supply further information about exclusions from the endpoint analysis, treatment discontinuations, adherence, or participant flow. It is therefore not possible to assess from these registry entries alone how completely the analysis retained randomized participants or how the results compare across alternative populations.

The registry identifies ANCOVA covariates and reports the use of an adjusted model, but does not report diagnostic checks, model coefficients, the detailed imputation procedure, or the non-inferiority margin and decision rule. For time-to-event outcomes, full censoring rules and details of the multiple listed estimates are also not reported. These omissions matter because they affect reproducibility and interpretation, not because they prove that the analyses were inappropriate.

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: end stage renal disease (27.6%), pneumonia (6.5%), acute kidney injury (3.9%), acute myocardial infarction (3.9%), cardiac failure congestive (3.6%).

The registry lists serious adverse events affecting 504 participants in the vadadustat group and 488 in the darbepoetin alfa group, with the corresponding groups at risk listed as 861 and 862. Other adverse events affected 482 and 436, with the same respective at-risk counts. Deaths are listed as 139 in each group. These are posted counts, not adjusted comparisons. The registry entries do not provide a statistical comparison, follow-up-adjusted rate, or detailed account of how the at-risk populations were defined for each safety measure.

The most frequently listed serious-event terms include end stage renal disease (27.6%), pneumonia (6.5%), acute kidney injury (3.9%), acute myocardial infarction (3.9%), cardiac failure congestive (3.6%), and urinary tract infection (2.3%). The registry does not state the denominator or additional detail needed to reinterpret these percentages, so they should be read as the posted values rather than converted into participant counts or comparative risks.

Serious adverse event counts do not by themselves establish causation or show whether one treatment has a higher risk. Differences in exposure time, event definitions, and reporting can matter; the detailed information needed to assess those factors is not reported in the registry record. These safety figures describe what is posted and should not be used as a medical recommendation.

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

The primary result describes estimated average change in Hb over Weeks 24 to 36 for randomized participants assigned to vadadustat or darbepoetin alfa. The sponsor’s adjusted estimates are close, and the reported confidence interval for their difference spans zero. This means the estimate is uncertain over a range that includes differences in either direction. The unadjusted re-calculation also does not show a clear difference, but it is not the sponsor’s adjusted analysis.

The result does not show that the treatments are identical. A failure to distinguish groups in a conventional difference test is not a demonstration of equivalence. Nor does the posted confidence interval alone establish non-inferiority: that interpretation requires the prespecified margin and testing rule. Those details are not reported in the registry record.

The endpoint focuses on a laboratory measure during specified efficacy periods. The secondary outcomes include cardiovascular and other time-to-event measures, but their results do not establish a complete picture of all benefits and harms. The registry’s safety counts are descriptive and do not, by themselves, show that an event was caused by treatment or provide a risk-adjusted comparison.

These findings apply to the study population and analysis as recorded. The registry entries do not support extrapolation to populations or treatment settings not described in the registry record. Details about eligibility, dosing, participant flow, adherence, missingness, and the analysis plans are limited or not reported, so the boundaries of generalizability cannot be fully assessed.

In general, a statistical result is one part of evidence interpretation. Effect size, precision, study design, analysis assumptions, missing data, outcome selection, safety information, and clinical context all matter. The registry record supports a careful description of the posted estimates; it does not justify medical advice or a broad claim that either treatment works or does not work.

18. Why This Trial Matters Statistically

This study illustrates why a result close to zero and a non-significant difference are not enough to establish equivalence or non-inferiority. The sponsor’s primary estimate is reported as a non-inferiority analysis, but the margin and decision rule are absent from the registry record. Statistical interpretation depends not only on the point estimate, but also on the interval and the prespecified threshold against which that interval is judged.

It also demonstrates the importance of distinguishing an adjusted sponsor analysis from an unadjusted re-calculation. Both are based on posted trial results, but they answer the comparison using different methods. The sponsor’s ANCOVA with multiple imputation is the primary reported approach, while the re-calculation is a supplementary check based on summary statistics. Keeping those roles distinct prevents an approximate calculation from being mistaken for the trial’s planned inference.

The record also highlights how endpoint choice shapes interpretation. A laboratory outcome averaged over an efficacy period is not interchangeable with time-to-event outcomes, and hazard ratios are not direct summaries of mean Hb change. Multiple secondary analyses introduce further interpretive challenges when their distinctions and multiplicity handling are not reported.

Finally, posted safety counts and confidence intervals are informative only within their definitions and analysis context. A registry record can make key estimates accessible while leaving important details unavailable. Transparent reporting of margins, analysis plans, missing-data procedures, and outcome hierarchies is essential for readers to assess what a trial’s results establish and how precisely they do so.

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 trial-specific reporting gaps constrain interpretation. The non-inferiority margin and the sponsor’s full testing rule are not reported in the registry record. Without them, the primary estimate cannot independently establish whether the intended non-inferiority criterion was met. The registry also does not report the original sample-size rationale, so the planning illustrations based on observed effects cannot be treated as evidence about the trial’s design power.

The primary analysis description names ANCOVA, multiple imputation, and covariates, but does not include details of the imputation model, the amount and pattern of missing data, or sensitivity analyses. The method’s assumptions therefore cannot be evaluated. Although the population is described as all randomized participants, further information about participant flow, endpoint availability, treatment exposure, and exclusions is not reported in the registry record.

For some time-to-event outcomes, more than one hazard-ratio estimate is listed, but the registry record does not explain how those analyses differ. Detailed censoring rules, model specifications, and the handling of competing events are not fully reported. This limits the ability to reproduce or compare those results.

The record lists multiple secondary endpoints but does not report whether multiplicity was controlled or describe an inferential hierarchy. Open-label treatment assignment is reported, but procedures addressing possible effects on care or outcome reporting are not described. The safety information is presented as counts and selected event-term percentages; exposure-adjusted rates and detailed comparative analyses are not reported. These limitations identify what cannot be assessed from the registry record; they do not by themselves demonstrate that the study was conducted improperly.

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 Non-dialysis-dependent Chronic Kidney Disease (NDD-CKD) — NCT02680574.
• Registry record last updated 2022-06-27; status last verified 2022-06.
• Results first posted 2022-06-27.
• 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

NCT02680574 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 NDD-CKD. The registry lists enrollment as 1725, a start of 2016-02, and primary completion on 2020-06-18.

The primary endpoint was change from baseline in Hb averaged over Weeks 24 to 36. The sponsor reports a least-squares mean difference of -0.01, with a 95% confidence interval from -0.09 to 0.07, in an analysis classified as non-inferiority. The non-inferiority margin and full decision rule are not reported in the registry record. A simple unadjusted re-calculation is supplementary and does not replace the sponsor’s adjusted analysis.

Secondary Hb and time-to-event outcomes and descriptive safety counts are also posted. Their interpretation is limited by unreported multiplicity procedures, missing-data details, and some time-to-event analysis specifications.