Study to Evaluate Vadadustat for the Correction of Anemia in Participants With Non-dialysis-dependent Chronic Kidney Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate Vadadustat for the Correction of Anemia in Participants With Non-dialysis-dependent Chronic Kidney Disease (NCT02648347), 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

The trial asked whether oral vadadustat could correct anemia and maintain hemoglobin in participants with non-dialysis-dependent chronic kidney disease, compared with darbepoetin alfa. The primary endpoint was change from baseline in hemoglobin averaged over Weeks 24 to 36. The registry also reports hemoglobin change over Weeks 40 to 52 and several time-to-event outcomes concerning cardiovascular events, heart failure hospitalization, thromboembolic events, cardiovascular death, and all-cause mortality.

The primary endpoint is a laboratory measure of anemia correction rather than a direct measure of symptoms or longer-term clinical events. The posted results include a sponsor-reported non-inferiority analysis, but the non-inferiority margin is not reported in the registry record. Consequently, the estimate and its confidence interval can be described, but the margin-based criterion cannot be independently assessed from this record alone.

3. Trial Design

This was a Phase 3, randomized, open-label, active-controlled, parallel-group study. It compared vadadustat with darbepoetin alfa in participants with non-dialysis-dependent chronic kidney disease and anemia. The registry describes the study as multicenter and states that its purpose was correction of anemia and maintenance of hemoglobin. The record lists 1,751 participants enrolled and a randomized population for the primary analysis.

Randomization assigns participants to treatment groups by chance, which is intended to make groups comparable at the start with respect to both measured and unmeasured characteristics. The primary analysis followed randomized treatment assignment, rather than describing participants only according to treatment received. The record says analyses of the randomized population were based on randomized treatment.

The study was open-label, meaning masking was listed as none. Participants and study personnel therefore were not described as blinded to assignment. This feature is particularly relevant when outcomes involve judgment or reporting; hemoglobin is a laboratory measure, while the secondary outcomes include clinical events. The registry record does not report further procedures for event adjudication or masking of outcome assessors.

The primary endpoint was change from baseline in hemoglobin averaged over Weeks 24 to 36. A secondary hemoglobin endpoint used Weeks 40 to 52. Other secondary outcomes included time to first cardiovascular MACE, time to cardiovascular death, time to all-cause mortality, and a broader composite that included MACE plus heart failure hospitalization or a thromboembolic event excluding vascular access thrombosis. The record lists a completed study and a primary completion date of 2020-06-04. Additional detail about recruitment locations, treatment duration, dosing, protocol amendments, and the original design assumptions is not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 4708 participants were screened for entry into the study. Of these, 1751 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 measures the average change in hemoglobin concentration from baseline to the primary efficacy period, Weeks 24 to 36. Hemoglobin is reported in g/dL. The baseline value was defined as the average of values at the screening visit closest to randomization and at the randomization visit. The endpoint-period value was the average hemoglobin over Weeks 24 to 36.

Using an average over a defined period gives a measure of hemoglobin during that window rather than relying on a single visit. In general, averaging repeated measurements can help represent the level over the period and reduce the influence of an unusually high or low measurement. That general rationale does not establish how often measurements were taken in this trial; the schedule beyond the stated visits and period is not reported in the registry record.

This endpoint is used to assess correction of anemia through a measurable change in hemoglobin. It does not by itself establish how participants felt, functioned, or experienced clinical events. Those questions require other outcomes. The posted analysis reports least-squares means and a sponsor-reported difference with a 95% confidence interval. The registry labels the sponsor analysis as non-inferiority, but its margin and detailed decision rule are not reported in the registry record.

7. Results Posted in the Registry

• Darbepoetin Alfa: mean 1.38 versus 1.43 on control; difference -0.05 (95% CI -0.18 to 0.08), standardized effect d = -0.04; z-test p = 0.447.

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 1.48 versus 1.52 on control; difference -0.04 (95% CI -0.19 to 0.11), standardized effect d = -0.03; z-test p = 0.590.
• 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 1.16 (95% CI 0.97–1.38), reported p = =0.1743 (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 1.19 (95% CI 0.90–1.56), reported p = =0.3154 (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.

Across the posted secondary outcomes, the hemoglobin estimates remain close between treatment groups, while the cardiovascular and broader event outcomes have hazard-ratio estimates above 1 and confidence intervals that include 1. These results do not provide a clearly separated pattern across the secondary endpoints. The event outcomes also have less precision than the primary continuous hemoglobin endpoint, consistent with the smaller event counts reported for those analyses.

The secondary hemoglobin result is directionally consistent with the primary result in the sense that both sponsor-reported differences are small and their confidence intervals include zero. This resemblance adds context, but it does not replace the primary analysis or establish a separate conclusion about the secondary period. The time-to-event outcomes address different questions from hemoglobin change and should not be treated as direct confirmations or refutations of the primary endpoint.

Secondary outcomes are generally interpreted with caution when many outcomes or analyses are considered. Testing multiple endpoints increases the chance that at least one apparently notable result could arise by chance. A prespecified multiplicity adjustment can address that issue, but such a procedure is not reported in the registry record. The registry reports two analyses for some event outcomes, without explaining how they differ. Without the full analysis plan and multiplicity strategy, the secondary results are best treated as supporting context rather than as a set of independent confirmatory findings.

The registry lists additional secondary outcomes, including cardiovascular death and all-cause mortality, but the record does not provide numerical results for them in the summaries available for this analysis. Their results and any corresponding uncertainty are not reported in the registry record. No conclusion about those outcomes should be inferred from the results of the other secondary endpoints.

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 registry reports an analysis of covariance (ANCOVA) for the primary hemoglobin endpoint, with multiple imputation for missing data. ANCOVA compares groups on a continuous outcome while adjusting for specified covariates. In general, adjustment can account for chance differences in those covariates and can improve precision when they are related to the outcome. The covariates listed for this analysis were baseline hemoglobin category (<9.5 versus ≥9.5 g/dL), geographic region (United States, European Union, or Rest of World), and New York Heart Association congestive heart failure class (Class 0 or I versus Class II or III). The registry record does not report further details about model diagnostics or how the covariate terms were parameterized.

What do least-squares means represent?

Least-squares means are model-adjusted group estimates. Rather than simply taking each group's raw average, the model estimates the outcome for each treatment group while accounting for the covariates included in the analysis. Their difference is therefore an adjusted contrast. The sponsor's primary analysis reports a least-squares mean difference of 0.05 g/dL. The registry record does not provide the full model output or additional details needed to reproduce that adjusted estimate independently.

Why use multiple imputation?

Multiple imputation is a general statistical approach for handling missing measurements. It creates multiple plausible completed datasets using an imputation model, analyzes each dataset, and combines the results to reflect both within-dataset uncertainty and uncertainty about missing values. It relies on assumptions about the missingness process and the imputation model. The registry says multiple imputation was used for missing primary endpoint data, but the imputation variables, number of imputations, and sensitivity analyses are not reported in the registry record. Those details matter when judging how dependent results may be on assumptions about missing data.

How should the unadjusted recalculation be read?

The recalculated comparison is a simple, unadjusted comparison based on the posted group summaries. It uses the displayed least-squares means and standard errors as summary inputs, with an approximate pooled standard deviation noted for the calculation. It is not a reconstruction of the sponsor's ANCOVA model or its multiple-imputation procedure. The resulting estimate, confidence interval, and p-value therefore answer a simpler question and can differ from the sponsor's adjusted analysis. In this case, the recalculated mean difference is -0.05 g/dL when stated as darbepoetin alfa relative to vadadustat; the sponsor's reported contrast uses the reverse direction and is adjusted.

General explanation: a standard error describes the estimated sampling variability of an estimate. It is not the spread of individual participant measurements. The registry reports standard errors for the least-squares means, while the recalculation also uses an approximate pooled standard deviation. Because the pooled standard deviation is estimated from the displayed summaries, the recalculated quantities should be read as approximate and unadjusted.

How are time-to-event outcomes analyzed?

Time-to-event analyses consider both whether an event occurred and how long it took to occur, while accounting for participants whose event time is not observed during follow-up. The registry reports hazard ratios with 95% confidence intervals for the posted secondary event outcomes. A hazard ratio compares event rates over follow-up under the model or method used; it is not a ratio of the reported medians. In general, a value of 1 corresponds to no relative difference in the modeled event rate, while values on either side indicate different estimated directions. Confidence intervals that include 1 leave uncertainty about whether the data distinguish the groups on that measure.

The broader composite outcome lists Log Rank as the method for its two reported analyses. The cardiovascular MACE outcome lists Gray's Test. The registry gives two hazard-ratio analyses for each of these outcomes but does not explain in the record how the two analyses differ. Their estimates should therefore be reported as posted rather than assigned an unreported interpretation or analysis population. Median event times are also reported with intervals; a median time is the time by which half of the relevant event-time distribution has experienced the event, under the analysis definition. It is distinct from a hazard ratio.

What does over-dispersion mean in general?

General explanation: over-dispersion occurs when the observed variability in data is greater than a statistical model assumes. It can make standard errors too small if not accounted for, causing confidence intervals to be too narrow and tests to appear more decisive than warranted. The primary endpoint is continuous and analyzed with ANCOVA; the registry does not report an over-dispersion adjustment for that model, and no claim that over-dispersion occurred is supported by the registry record.

The trial's original sample-size justification, power assumptions, interim analyses, prespecified multiplicity procedure, and detailed statistical analysis plan are not reported in the registry record. The separate planning illustrations are based on observed effects and stated generic assumptions; they are not evidence of the original trial's design rationale.

11. Confidence Intervals and Precision

A confidence interval expresses uncertainty around an estimated effect. In general, a 95% confidence interval is produced by a procedure that, across repeated applications under its assumptions, would contain the underlying quantity in 95% of cases. It is not a guarantee that a particular interval contains the true value, nor does it assign a probability to the true value after the interval has been observed.

For the primary endpoint, the sponsor-reported difference is 0.05 g/dL and its 95% confidence interval ranges from -0.04 to 0.15. The interval spans zero, so the estimate does not precisely establish the direction of a difference. Its endpoints also show that a range of effect sizes remains compatible with the analysis. The interval is for the adjusted least-squares mean difference reported by the sponsor, not for an unadjusted raw difference.

The unadjusted recalculation has a wider interval, from -0.179 to 0.079, around the reversed-direction estimate of -0.05 g/dL. That interval also spans zero. Differences between the sponsor interval and the recalculated interval are expected to be possible because the analyses use different approaches: one is adjusted and includes multiple imputation, while the recalculation uses posted summaries without adjustment. The recalculation is not a substitute for the sponsor's analysis.

For time-to-event outcomes, a hazard-ratio interval that includes 1 includes the value associated, in general, with no relative difference in the hazard. The reported event-outcome intervals are not narrow enough to support a highly precise distinction between groups. In general, greater event counts can improve precision, while sparse event data tend to yield wider intervals. The registry reports event counts within the endpoint summaries but does not report a formal precision target for each secondary outcome.

Precision is separate from importance. A confidence interval describes statistical uncertainty under a model and its assumptions; it does not by itself determine whether a difference is clinically meaningful. The registry's non-inferiority margin is not reported in the registry record, so the precision of the estimate cannot be judged against that criterion.

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 original trial's design assumptions. For continuous outcomes, the displayed quantities are participants per arm. For time-to-event outcomes, the quantities are total events, not participants. They assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation for the planning calculations; the effect to detect is the stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld approach.

The 80% power column gives the planned number of participants per arm, or total events for time-to-event outcomes, under which a study would have an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column gives the corresponding planning quantity for a 90% chance. These are design concepts: power describes the long-run performance of a planned test under stated assumptions, not the probability that a particular result is true.

Rows that plan for 75% or 50% of the observed effect assume a smaller effect than the observed estimate. Smaller effects are harder to distinguish from random variation, so they require more participants or events for the same target power. The displayed figures are consequently sensitive to the observed effect used as their starting point; when an observed effect is close to zero, planning around a fraction of it can produce very large requirements. These illustrations are not observed power, and they do not establish what enrollment the trial originally intended or needed.

For example, the primary hemoglobin illustration is expressed in participants per arm, whereas the event-outcome illustrations are expressed in total events. Those quantities should not be compared as though they were the same unit. The trial's own sample-size justification and design assumptions are not reported in the registry record.

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 = -0.050; pooled standard deviation σ = 1.376.
2. n = 2 × (1.96 + 0.842)² × 1.376² / -0.050² = 11,886.2, rounded up to 11,887 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 <- -0.05                      # observed difference in means
sigma <- 1.3758536827016                     # 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(2648347)
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 = 11,887 (80% power), 15,913 (90% power)
 75% of observed effect: n per arm = 21,131 (80% power), 28,289 (90% power)
 50% of observed effect: n per arm = 47,545 (80% power), 63,649 (90% power)
power.t.test: 11887.1 
Simulated power at n = 11,887 per arm: 0.803 (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 primary analysis is the reported adjusted non-inferiority analysis: a least-squares mean difference of 0.05 g/dL, with a 95% confidence interval from -0.04 to 0.15. Its method is described as ANCOVA with multiple imputation for missing data and adjustment for baseline hemoglobin category, geographic region, and NYHA congestive heart failure class. The registry record does not report a p-value for this analysis.

The recalculation is a separate, simple, unadjusted comparison using the posted summary statistics. It gives -0.05 g/dL when expressed as darbepoetin alfa relative to vadadustat, with a 95% confidence interval from -0.179 to 0.079 and an unadjusted p-value of 0.447. The contrast direction differs from the sponsor's: the sponsor's positive estimate is vadadustat relative to darbepoetin alfa. The recalculation also does not reproduce the adjustment or missing-data procedure used in the sponsor analysis.

Because the registry record does not flag a discrepancy between the posted summaries and the sponsor's result, the recalculation is best read as a transparent unadjusted check rather than as a replacement. The sponsor analysis remains the trial's reported analysis. The registry's non-inferiority label does not supply the missing margin or full decision rule; those are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators evaluate more than one endpoint, comparison, time point, or analysis. In general, the more statistical tests performed, the greater the opportunity for chance findings unless the analysis plan controls the overall error rate or otherwise explains how results will be interpreted. The registry lists multiple secondary endpoints and reports more than one analysis for some time-to-event outcomes. A multiplicity strategy, including any adjustment or hierarchy among endpoints, is not reported in the registry record. The secondary p-values should therefore not be read as though they were necessarily protected by a single confirmatory testing plan.

Missing data are relevant to the primary endpoint because the registry says multiple imputation was used. Multiple imputation can incorporate uncertainty about missing values, but its validity depends on the model and assumptions. The record does not report the imputation model, the number of imputed datasets, reasons for missing measurements, or sensitivity analyses under alternative assumptions. Those details limit independent assessment of robustness to missingness.

The primary analysis population is described as all randomized participants, with analyses based on randomized treatment. That is an intention-to-treat-style assignment principle, but the registry's exact handling of participants with no usable endpoint data is not reported in the registry record. The secondary event analyses have endpoint-specific numbers, which are smaller than total randomized enrollment; the record does not provide enough detail to describe all censoring, eligibility, or analysis-set rules.

The registry identifies the primary outcome as a non-inferiority analysis, but the non-inferiority margin and the full prespecified decision rule are not reported in the registry record. The original sample-size assumptions, interim analysis plan, and detailed statistical analysis plan are also not reported in the registry record. These omissions prevent a complete assessment of how the reported analysis relates to the original protocol and its planned error control.

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 (33.6%), pneumonia (6.8%), acute kidney injury (4.8%), cardiac failure congestive (4.6%), fluid overload (3.9%).

The registry reports serious adverse events affecting 573 of 878 participants in the vadadustat group and 561 of 870 participants in the darbepoetin alfa group. It also reports other adverse events affecting 561 of 878 and 565 of 870, respectively. Death counts are reported as 180 in the vadadustat group and 168 in the darbepoetin alfa group. These are counts of participants reported in each category, not estimates of a causal treatment effect.

The listed serious adverse event terms include End stage renal disease (33.6%), Pneumonia (6.8%), Acute kidney injury (4.8%), Cardiac failure congestive (4.6%), Fluid overload (3.9%), and Acute myocardial infarction (3.6%). The registry excerpt does not specify the denominators or whether these percentages are pooled across groups or otherwise defined; that detail is not reported in the registry record. They should not be interpreted as group-specific risks from the information.

Serious adverse event counts and event-term frequencies provide a descriptive safety overview, but they do not alone establish whether treatment caused an event or whether groups differ reliably. The open-label design, event definitions, follow-up, exposure, and statistical comparisons all matter. Further detail about causality assessment and comparative safety analyses is not reported in the registry record.

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

The posted results describe a randomized comparison of vadadustat and darbepoetin alfa in people with anemia and non-dialysis-dependent chronic kidney disease. For the primary hemoglobin endpoint, the sponsor reported an adjusted difference of 0.05 g/dL, with a 95% confidence interval from -0.04 to 0.15. The interval includes zero, leaving uncertainty about the direction and size of the difference. The posted group estimates were 1.43 g/dL and 1.38 g/dL for vadadustat and darbepoetin alfa, respectively.

The registry identifies the primary analysis as non-inferiority, but the margin and decision rule are not reported in the registry record. The estimates therefore cannot, by themselves, establish whether the prespecified non-inferiority criterion was satisfied. Nor does a close average change establish that the treatments have identical effects for every participant or on every outcome.

The hemoglobin result concerns a laboratory measure averaged over a specified period. It does not directly answer questions about symptoms, daily functioning, long-term kidney outcomes, or all cardiovascular outcomes. The secondary event estimates are imprecise and should be interpreted separately from the primary endpoint. The safety counts are descriptive and do not establish causation.

More broadly, statistical estimates summarize the data under particular models and assumptions. Their interpretation depends on missing-data handling, outcome definitions, analysis populations, multiplicity procedures, and the prespecified non-inferiority framework. Several of these details are not reported in the registry record. The results should therefore be understood as the posted trial analyses and summaries, not as a complete account of every protocol or clinical consideration.

18. Why This Trial Matters Statistically

This trial offers a useful example of how different statistical questions can coexist within one randomized study. Its primary outcome is a continuous laboratory measure analyzed with covariate adjustment and multiple imputation, while several secondary outcomes are time-to-event analyses. Those methods produce different effect measures and require different kinds of interpretation.

The results also illustrate why an estimate should be read together with its confidence interval. The primary point estimate is small, but the interval includes values on both sides of zero. The sponsor's non-inferiority label requires a margin-based interpretation, yet that margin is not reported in the registry record. A label alone cannot substitute for the information needed to assess the decision rule.

The comparison between the sponsor analysis and the unadjusted recalculation is another important statistical lesson. Adjustment, missing-data methods, and the direction in which a contrast is expressed affect how an estimate is defined and presented. A simple recalculation can serve as a check on the posted summaries, but it does not recreate a more complex sponsor analysis.

Finally, multiple secondary endpoints and event analyses require restraint in interpretation. Their estimates add context, but without a reported multiplicity plan, they should not be treated as a collection of independent confirmatory tests. Together, these features make the study a practical case for distinguishing design, analysis, precision, and the limits of registry reporting.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the non-inferiority margin, so the sponsor's non-inferiority conclusion cannot be assessed against its criterion from the available information. It also does not report the original sample-size justification, interim analysis plan, or detailed statistical analysis plan. Important details of the multiple-imputation procedure and sensitivity analyses are likewise not reported in the registry record.

The study was open-label, with masking listed as none. The primary outcome is a laboratory measure, but the record does not state whether outcome assessors were masked. Event adjudication procedures and the definitions used for the reported time-to-event analyses are not described in the information available for this analysis. The registry reports two hazard-ratio analyses for some endpoints without explaining their differences.

The posted secondary results are incomplete in the summaries available for this analysis: numerical results for cardiovascular death and all-cause mortality are not reported in the registry record. The serious adverse event term percentages are listed without the relevant denominator or group-specific breakdown in the record. Exposure duration, dosing details, and additional safety comparison methods are also not reported in the registry record.

The simple recalculation is unadjusted and based on summary statistics; it cannot reproduce the sponsor's ANCOVA with multiple imputation. It is therefore a limited cross-check, not an alternative definitive analysis. The precision and interpretation of results also depend on assumptions and analysis details that cannot be evaluated from the registry summary alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate Vadadustat for the Correction of Anemia in Participants With Non-dialysis-dependent Chronic Kidney Disease — NCT02648347.
• 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

The registry describes a completed Phase 3, randomized, open-label, active-controlled, parallel-group study of vadadustat versus darbepoetin alfa for anemia correction and hemoglobin maintenance in non-dialysis-dependent chronic kidney disease. Enrollment was 1,751. The primary outcome was change from baseline in hemoglobin averaged over Weeks 24 to 36, analyzed in the randomized population using ANCOVA with multiple imputation.

The sponsor-reported primary least-squares mean difference was 0.05 g/dL, with a 95% confidence interval from -0.04 to 0.15. The registry labels the analysis non-inferiority, but the margin is not reported in the registry record. Secondary outcomes include hemoglobin change over Weeks 40 to 52 and several cardiovascular and mortality time-to-event measures. The record also reports adverse event counts and selected serious-event terms. Interpretation is limited by missing details on the original design assumptions, multiplicity, missing-data procedures, and some secondary results.