Vadadustat for the Prevention and Treatment of Acute Respiratory Distress Syndrome (ARDS) in Hospitalized Patients With Coronavirus Disease 2019 (COVID-19): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Vadadustat for the Prevention and Treatment of Acute Respiratory Distress Syndrome (ARDS) in Hospitalized Patients With Coronavirus Disease 2019 (COVID-19) (NCT04478071), a randomized phase 2 study. The primary outcome is Number of Participants Who Are Classified 8 (Dead), 7 (Hospitalized, on Invasive Mechanical Ventilation or ECMO), or 6 (Hospitalized, on Non-invasive Ventilation or High Flow Oxygen Devices) on the NIAID Ordinal Scale.

2. Clinical Question

3. Trial Design

The registry identifies this as a phase 2, randomized, quadruple-masked, parallel-group trial of vadadustat and placebo in hospitalized patients with COVID-19. The sponsor was The University of Texas Health Science Center, Houston. The record reports enrollment of 448 and a completed study. Its listed start date is 2020-08-22, and its primary completion date is 2022-03-07.

Random allocation means that assignment to the two groups was intended to be determined by chance, rather than by a clinician or participant choosing a group. In a parallel-group design, participants are assigned to one group and outcomes are compared between groups. The record labels masking as quadruple but does not identify which roles were masked or describe how masking was maintained. The reported information therefore supports describing the design using those registry labels, but not supplying operational details that are absent.

The primary outcome was assessed at day 14 and counted participants in NIAID Ordinal Scale categories 6, 7, or 8. The registry also lists 13 outcome measures and 4 analyses, while only 1 secondary outcome is posted in the results. The record does not report the original design assumptions, the full protocol, or a detailed analysis plan. It also does not report how participants were selected for each outcome analysis or explain why the analysis denominators differ from the enrollment figure.

The primary comparison uses the vadadustat group against placebo. The posted group counts are 43 of 216 for vadadustat and 53 of 223 for placebo. These outcome-specific counts are not a substitute for a participant-flow account; the registry record does not report a complete account of screening, exclusions, follow-up, or missing outcome data.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Who Are Classified 8 (Dead), 7 (Hospitalized, on Invasive Mechanical Ventilation or ECMO), or 6 (Hospitalized, on Non-invasive Ventilation or High Flow Oxygen Devices) on the NIAID Ordinal Scale, measured over day 14.

The primary endpoint counts participants classified at day 14 in categories 6, 7, or 8 on the National Institute of Allergy and Infectious Disease Ordinal Scale. Category 6 denotes hospitalization with non-invasive ventilation or high-flow oxygen devices; category 7 denotes hospitalization with invasive mechanical ventilation or ECMO; and category 8 denotes death. The scale also lists less severe states, ranging from hospitalization without supplemental oxygen to not being hospitalized without activity limitations, but those states are not included in this primary endpoint.

Combining the three specified categories creates a binary outcome for this comparison: each participant is either counted in one of those categories or is not. This can make a comparison of a severe clinical status easier to interpret than a comparison across every ordinal category, but it also discards distinctions among the included states. Death, invasive ventilation, and non-invasive ventilation or high-flow oxygen are not identical outcomes. The combined count does not show which category accounts for the group result, nor does it describe changes before or after day 14.

The registry record uses a participant count as the measure and specifies day 14 as the timeframe. It does not report further rationale for selecting this endpoint, the approach to participants whose day 14 status was unavailable, or whether other analyses of the ordinal scale were prespecified.

7. Results Posted in the Registry

• Vadadustat: 19.9% (43/216) versus 23.8% (53/223) on control; risk difference -3.9 percentage points (95% CI -11.6 to 3.9), risk ratio 0.84 (0.59–1.20); unadjusted two-proportion z-test p = 0.328.

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.

Number of Participants With a Total Score of 0 on the Modified Sequential Organ Failure Assessment (MSOFA) Scale

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Vadadustat: 72.9% (156/214) versus 70.4% (157/223) on control; risk difference 2.5 percentage points (95% CI -6.0 to 10.9), risk ratio 1.04 (0.92–1.17); unadjusted two-proportion z-test p = 0.563.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vadadustat and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 13 outcome measures but posts one secondary outcome in the results: the number of participants with a total score of 0 on the MSOFA scale at day 14. Consequently, there is not a broad set of posted secondary results from which to describe a pattern across different outcomes. The secondary comparison does not show a clear separation between groups in its reported risk ratio, posterior probability, or recalculated risk difference.

This result is directionally consistent with the primary result in the limited sense that neither posted comparison provides clear evidence of a group difference. It does not independently confirm the primary finding or establish that the groups are equivalent. The outcomes measure different things: the primary outcome counts participants in specified severe NIAID Ordinal Scale categories, whereas the secondary outcome counts participants with an MSOFA total score of 0. Their estimates should not be pooled or treated as interchangeable.

Secondary findings generally carry less weight when many outcomes or analyses are considered, unless the analysis plan accounts for that multiplicity. Examining many outcomes increases the chance of finding an apparently notable result by chance. The registry reports 13 outcome measures and 4 analyses, but the multiplicity approach and the relationship between those counts are not reported. The single posted secondary result should therefore be interpreted as supportive descriptive information, not as a stand-alone basis for a definitive conclusion about the primary question. No adjustment for multiplicity is reported in the registry record.

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

• Number of Participants With a Total Score of 0 on the Modified Sequential Organ Failure Assessment (MSOFA) Scale

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint, a participant is classified as having or not having the event defined by the analysis. Here, the primary event is being in NIAID Ordinal Scale category 6, 7, or 8 at day 14. The posted counts and denominators allow the registry to report a comparison between the event proportions in the two groups. A count alone does not indicate the comparative size of an effect, so the analysis also uses measures such as a risk difference or risk ratio.

What does a risk difference express?

In general, a risk difference subtracts the event proportion in one group from the event proportion in the other. In the recalculated primary comparison, the difference is expressed as vadadustat minus placebo. A negative estimate indicates a lower observed event proportion in the vadadustat group; a positive estimate indicates a higher one. The estimate is a measure of the observed contrast, not a proof that treatment caused the difference. Interpretation also depends on the trial design, the outcome definition, missing data, and the analysis method.

The recalculated primary risk difference is -0.039. Its interval runs from -0.116 to 0.039. The recalculated secondary risk difference is 0.025, with an interval from -0.059 to 0.109. These are simple unadjusted recalculations from the posted summary statistics. They are not adjusted for additional participant characteristics or for multiple outcomes. The registry record does not report whether the sponsor’s primary analysis used adjustment or other modeling choices.

What does a risk ratio express?

In general, a risk ratio compares the event proportion in one group with the event proportion in another by division. A ratio of 1 represents equal observed proportions; a value above or below 1 indicates a higher or lower proportion in the numerator group, according to the comparison’s orientation. The registry reports a secondary risk ratio of 1.01, with a 95% confidence interval from 0.92 to 1.1. The primary recalculation also includes a risk ratio of 0.838, with a 95% confidence interval from 0.587 to 1.196. These relative measures and risk differences describe the same binary outcome from different perspectives; neither alone resolves uncertainty about the result.

How should the p-values be read?

In general, a p-value describes how compatible the observed data are with a specified null model, 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 recalculated unadjusted primary p-value is 0.328 and the secondary p-value is 0.563. The registry does not post p-values for the sponsor’s reported analyses. These recalculated p-values should not be substituted for the sponsor’s analysis or treated as the complete analysis plan.

What does a confidence interval contribute?

In general, a confidence interval gives a range of estimates compatible with the data under the method’s assumptions. Its width conveys precision: a wider interval leaves more uncertainty about the size and direction of the effect. An interval that includes zero for a risk difference, or 1 for a risk ratio, includes the value corresponding to no difference on that scale. It does not prove there is no effect, and it does not mean that every value inside the interval is equally plausible. The recalculated and sponsor-reported primary intervals include zero, and the secondary risk-ratio interval includes 1.

The sponsor also reports posterior probability values of 0.94 for the primary outcome and 0.57 for the secondary outcome. In general, a posterior probability depends on a statistical model and prior assumptions and represents probability conditional on those assumptions and the observed data. The registry record does not report the model, prior, or precise probability statement for these results. They should therefore be read as registry-reported summaries, not as interchangeable with frequentist confidence intervals or p-values.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than a model assumes. It can make standard errors too small and intervals too narrow if the extra variability is ignored. The primary outcome is posted as a binary count, and the registry record does not report a dispersion measure or a method addressing over-dispersion. No conclusion about whether over-dispersion was present or relevant in this trial can be drawn from the posted information.

The record identifies the primary measure, group counts, and some comparative estimates, but does not report the detailed sponsor analysis method, the analysis population definition, or missing-data procedures. The recalculated comparisons are useful as transparent, unadjusted contrasts of the posted summaries, while the sponsor-reported analysis remains the registry’s own reported analysis.

11. Confidence Intervals and Precision

Precision is about how narrowly the data locate a comparative effect. The recalculated primary risk difference is -0.039, and its 95% confidence interval extends from -0.116 to 0.039. This range includes zero, so the data are compatible with no difference on the risk-difference scale as well as with effects on either side of zero. The interval is broad enough that the point estimate alone would give an incomplete account of uncertainty.

The sponsor-reported primary risk difference is -0.036, with a 95% confidence interval from -0.084 to 0.009. This interval also includes zero. The registry does not report enough methodological detail to explain the difference in width between the sponsor-reported and recalculated intervals. Neither interval supports treating the point estimate as an exact measure of the underlying effect.

For the posted secondary outcome, the reported risk ratio is 1.01, with a 95% confidence interval from 0.92 to 1.1. The recalculated risk-difference interval runs from -0.059 to 0.109. Both measures leave uncertainty around the size and direction of the comparison. In general, confidence intervals quantify sampling uncertainty under their methods; they do not account automatically for every possible source of bias, missing data, outcome measurement issues, or multiplicity.

The intervals should not be read as the probability that the true effect lies within the particular interval. Nor does inclusion of the no-difference value establish equivalence. An equivalence or non-inferiority conclusion would require a prespecified margin and an analysis designed for that question; the registry record does not report such a margin or analysis. The posted results are most informative when estimates are considered together with their intervals and the limitations of the registry record.

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.

Each planning figure is a number of participants per arm, not a total across arms and not a count of events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. These are planning illustrations based on the observed effect, not the trial’s own original design assumptions; those original assumptions are not reported in the registry record.

The 80% power column means the participants per arm estimated, under those assumptions, for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations, not statements about the probability that the trial result is true. For the primary outcome, planning for 100% of the observed effect gives 1,798 participants per arm for 80% power and 2,407 participants per arm for 90% power. Planning for 75% gives 3,248 and 4,347 participants per arm, respectively; planning for 50% gives 7,420 and 9,932.

The secondary outcome planning figures follow the same interpretation: they give participants per arm for the specified effect fraction and target power. Smaller effects need more participants to detect under the same assumptions, which is why planning for a smaller fraction of the observed effect produces larger figures. These calculations are not observed power. They do not measure the chance that the completed trial detected an effect, and they do not establish whether the original trial was adequately designed. The registry record does not report the original sample-size justification.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.238; treatment proportion p₁ = 0.199; average p̄ = 0.218.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5843 = 1.1451.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5836 = 0.4912.
4. n = (1.1451 + 0.4912)² / (-0.0386)² = 1,797.7, rounded up to 1,798 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.237668161434978                          # control proportion
p1 <- 0.199074074074074                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4478071)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,798 (80% power), 2,407 (90% power)
 75% of observed effect: n per arm = 3,248 (80% power), 4,347 (90% power)
 50% of observed effect: n per arm = 7,420 (80% power), 9,932 (90% power)
power.prop.test: 1797.7 
Simulated power at n = 1,798 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

For the primary outcome, the sponsor-reported risk difference is -0.036, with a 95% confidence interval from -0.084 to 0.009, and the sponsor also reports a posterior probability of 0.94. The recalculated unadjusted risk difference is -0.039, with a 95% confidence interval from -0.116 to 0.039 and p = 0.328. Both risk-difference point estimates are negative, and both confidence intervals include zero. The registry does not mark a discrepancy between the reported analysis and the recalculation.

The two summaries are not identical. The registry record does not report the sponsor’s detailed statistical method, the assumptions behind the posterior probability, or enough information to determine why the confidence intervals differ. The recalculation is a simple unadjusted comparison from the posted group summaries; it is not a reproduction of an undocumented sponsor model. The sponsor-reported result should be understood as the registry’s own analysis, while the recalculation provides a separate, transparent summary of the posted counts.

For the secondary outcome, the sponsor-reported risk ratio is 1.01, with a 95% confidence interval from 0.92 to 1.1, and posterior probability 0.57. The recalculated unadjusted risk difference is 0.025, with a 95% confidence interval from -0.059 to 0.109 and p = 0.563. These estimates use different scales, so their numerical values should not be compared directly. Both sets of summaries leave uncertainty around the comparative result.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 13 outcome measures and 4 analyses, but it does not provide a complete account of how outcomes and analyses were selected or prioritized. Only one secondary outcome is posted in the results. The record does not report whether a multiplicity adjustment was planned or applied. When several outcomes or analyses are examined, the chance of at least one seemingly notable result can rise; adjustment procedures can address that issue, but no particular procedure should be assumed.

The record also does not report the analysis populations, such as whether the primary analysis followed all randomized participants, nor does it give a participant-flow description. Counts differ between the primary and secondary outcomes and their denominators differ, but the reason is not reported in the registry record. It is not possible to infer whether this reflects missing measurements, eligibility for an outcome, exclusions, or another analysis decision.

Missing-data handling is not reported in the registry record. The posted results do not describe how unavailable day 14 status or unavailable MSOFA scores were treated, whether any values were imputed, or what sensitivity analyses were conducted. These details matter because conclusions can depend on how missing outcome information is handled, particularly when missingness differs between groups or relates to outcome status.

The registry record does not report interim analyses, stopping rules, a detailed statistical analysis plan, or the original sample-size justification. It also does not specify a prespecified margin for equivalence or non-inferiority. These omissions limit assessment of whether the posted analyses reflect the planned primary analysis and how much flexibility existed in outcome selection or modeling. Absence of reporting does not establish that a procedure was or was not used; it means that the procedure cannot be assessed from the registry record.

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: worsening pneumonia (26.0%), septic shock (10.9%), alanine aminotransferase increased (4.4%), thromboembolic event (2.7%), acute kidney injury (1.8%).

The registry reports serious adverse events affecting 61 of 221 participants at risk in the vadadustat group and 73 of 227 at risk in the placebo group. Other adverse events affected 109 of 221 and 116 of 227, respectively. The registry also reports 19 deaths in each group. These are descriptive counts with the listed at-risk denominators; the record does not provide enough detail to establish whether events were judged related to study treatment or to support a causal comparison.

The serious adverse event terms most frequently listed include worsening pneumonia at 26.0%, septic shock at 10.9%, alanine aminotransferase increased at 4.4%, thromboembolic event at 2.7%, acute kidney injury at 1.8%, and atrial fibrillation with rapid ventricular response at 1.8%. The registry record does not specify the denominator or additional coding details for these term percentages in the posted information. They should not be interpreted as comparative risks without that context.

Safety counts require careful interpretation alongside the duration and completeness of follow-up, event definitions, and attribution procedures. Those details are not reported in the registry record. The figures describe the posted adverse-event results and do not establish that the intervention caused or prevented any listed event.

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

The primary data show fewer participants counted in the specified day 14 NIAID Ordinal Scale categories in the vadadustat group than in the placebo group. The recalculated risk difference is negative, and the sponsor-reported risk difference is also negative. However, both primary confidence intervals include zero, and the recalculated p-value is 0.328. The posted evidence therefore leaves uncertainty about the size and direction of the underlying between-group difference.

The results do not establish that vadadustat reduced the primary outcome, nor do they establish that the groups were identical. A non-significant or uncertain comparison is not proof of no effect. The posted secondary result likewise does not show a clear group separation, but it measures a different endpoint and is not a substitute for the primary outcome.

The endpoint combines death with two forms of respiratory support, so its count does not distinguish among the contributing clinical states. It is measured at day 14 and does not represent the complete course of illness. The record does not provide detailed information about missing outcomes, analysis populations, adjustment, or the sponsor’s full statistical methods. Those omissions constrain how confidently the estimates can be generalized or interpreted.

These findings are statistical descriptions of the registry record, not medical advice. They do not determine an individual treatment choice, establish a treatment mechanism, or answer questions about outcomes not reported in the posted results. A careful reading keeps the group counts, uncertainty intervals, endpoint definition, and incomplete reporting in view rather than relying on a single point estimate or probability summary.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should not be reduced to the difference between two observed counts. The primary counts are 43 of 216 and 53 of 223, but the effect estimate and its interval are needed to express the comparative magnitude and uncertainty. The recalculated and sponsor-reported risk differences are both negative, yet their confidence intervals include zero. That distinction between direction and precision is central to interpreting a clinical trial result.

The trial also shows how different statistical summaries answer different questions. Risk differences express an absolute contrast between group event proportions, while risk ratios express a relative comparison. A posterior probability is another type of summary and depends on assumptions that are not detailed in the registry record. These measures should be interpreted on their own scales and not treated as interchangeable evidence.

The endpoint itself is important to interpretation. Combining death and respiratory-support categories gives a binary count, but hides differences among the component states. The secondary MSOFA result does not replace the primary outcome, and the limited posted secondary results cannot establish a consistent pattern across all listed measures. Reporting the endpoint definition, analysis population, missing-data approach, multiplicity plan, and model details would make the evidence easier to evaluate.

Finally, planning calculations based on observed effects can illustrate the sample sizes associated with different effect targets, but they are not the original design rationale and are not observed power. Keeping planning assumptions distinct from trial results prevents a post hoc illustration from being mistaken for evidence about the strength of the completed study.

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 are specific to the information posted for this trial. The primary endpoint combines death, invasive mechanical ventilation or ECMO, and non-invasive ventilation or high-flow oxygen into one count. The registry does not report the counts separately for these categories, so the component driving the comparison cannot be identified from the posted primary result.

The primary group counts and denominators are outcome-specific, and the registry reports an enrollment figure of 448. It does not provide a participant-flow account or explain the difference between enrollment and the outcome denominators. The secondary outcome has different denominators, and the reason is also not reported. Without analysis-population definitions and missing-data handling, the effects of exclusions or unavailable outcome measurements cannot be assessed.

The sponsor’s detailed statistical method is not reported, and the record does not explain the posterior probability calculations. The sponsor’s primary interval and the recalculated unadjusted interval differ in width; the available information does not establish why. The multiplicity approach, interim analysis procedures, and original sample-size rationale are not reported. The trial’s registry label of quadruple masking does not specify who was masked or how.

Only one secondary outcome is posted despite the registry listing 13 outcome measures and 4 analyses. This limits assessment of the broader pattern of results and raises uncertainty about which outcomes were analyzed or reported. The safety information also lacks details about event attribution and the denominator context for listed serious-event term percentages. These limitations concern reporting and interpretation; they do not by themselves establish that the trial was conducted improperly.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Vadadustat for the Prevention and Treatment of Acute Respiratory Distress Syndrome (ARDS) in Hospitalized Patients With Coronavirus Disease 2019 (COVID-19) — NCT04478071.
• Registry record last updated 2025-03-26; status last verified 2025-03.
• Results first posted 2025-03-26.
• 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

NCT04478071 is a completed, randomized, quadruple-masked, parallel-group phase 2 trial sponsored by The University of Texas Health Science Center, Houston. It compared vadadustat with placebo in hospitalized patients with COVID-19 and reports enrollment of 448. The primary endpoint counted participants in NIAID Ordinal Scale categories 6, 7, or 8 at day 14. The sponsor-reported risk difference was -0.036, with a 95% confidence interval from -0.084 to 0.009; the recalculated unadjusted risk difference was -0.039, with a 95% confidence interval from -0.116 to 0.039. Both intervals include zero.

The registry posts one secondary outcome, the day 14 number of participants with an MSOFA score of 0. Its reported risk ratio was 1.01, with a 95% confidence interval from 0.92 to 1.1. The record does not report the detailed analysis plan, missing-data methods, analysis populations, or multiplicity approach. The posted results should be read as estimates with uncertainty and with those reporting limitations in mind.