Randomized Open Investigation Determining Steroid Dose: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized Open Investigation Determining Steroid Dose (NCT04834375), a randomized phase 3 study. The primary outcome is All Cause Mortality at 28 Days.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group trial with no masking. The registry lists an enrollment of 142 and identifies Northwell Health as the sponsor. The study is recorded as completed. Its recorded start date is 2021-03-19, and its primary completion date is 2022-01-25.

The two groups differed in dexamethasone dose. The standard group was assigned 6 mg intravenously each day for 10 days. The weight-based group was assigned 0.2 mg/kg/day intravenously, up to a maximum of 20 mg daily, for 10 days. The registry summary says the study compared the current standard dose with the higher weight-based dose in people with COVID-19 pneumonia.

For the primary outcome, the posted group sizes were 72 in the standard-dose group and 70 in the weight-based group. The outcome was all-cause mortality at 28 days. The registry comment also says participants were followed until the end of admission for final disposition, death or discharge. That additional follow-up explains why the number of deaths at discharge can differ from the number counted for the 28-day primary outcome.

The registry record does not report the original sample-size justification, detailed eligibility criteria, recruitment procedures, allocation concealment, or the planned statistical analysis. The record also does not report interim analyses. Those omissions do not show that a procedure was or was not used; they mean it cannot be characterized from 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.

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 All Cause Mortality at 28 Days, measured over 28 days.

The primary endpoint was all-cause mortality at 28 days, measured as a count of participants. It records whether a participant died from any cause within the stated follow-up window, rather than attributing death to a specific cause. In the posted results, the standard-dose group had 15 deaths among 72 participants, and the weight-based group had 12 among 70.

Mortality is a direct outcome that does not depend on judging whether a symptom or clinical change is important. A fixed time point also makes the groups’ outcome counts interpretable over the same stated period. More generally, using all-cause mortality avoids the additional judgment involved in deciding whether a death was caused by the condition or treatment under study.

The registry comment distinguishes the primary endpoint from final disposition at the end of admission: participants were followed until discharge or death for that final disposition. The 28-day outcome and end-of-admission deaths therefore refer to different follow-up definitions and should not be treated as interchangeable counts. The registry record does not report a more detailed primary-outcome population definition or a separate adjudication procedure.

7. Results Posted in the Registry

• Weight-based Dexamethasone Dose: 17.1% (12/70) versus 20.8% (15/72) on control; risk difference -3.7 percentage points (95% CI -16.6 to 9.2), risk ratio 0.82 (0.42–1.63); unadjusted two-proportion z-test p = 0.575.

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 Admitted to the ICU

• 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:
  • Weight-based Dexamethasone Dose: 17.1% (12/70) versus 37.5% (27/72) on control; risk difference -20.4 percentage points (95% CI -34.6 to -6.1), risk ratio 0.46 (0.25–0.83); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Weight-based Dexamethasone Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Days of Stay in the Intensive Care Unit

• 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 deviations.
• Result:
  • Weight-based Dexamethasone Dose: mean 11.33 versus 15.33 on control; difference -4.00 (95% CI -10.57 to 2.57), standardized effect d = -0.38; z-test p = 0.233.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Weight-based Dexamethasone Dose and the control. The interval gives the range of effects that remain compatible with the data.

Days of Hospitalization

• 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 deviations.
• Result:
  • Weight-based Dexamethasone Dose: mean 11.56 versus 14.83 on control; difference -3.27 (95% CI -7.71 to 1.17), standardized effect d = -0.24; z-test p = 0.149.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Weight-based Dexamethasone Dose and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address several aspects of illness and care: ICU admission and stay, hospitalization duration, oxygen supplementation, invasive ventilation and its duration, ECMO, and tracheostomy. This broad set provides context beyond the primary mortality endpoint, but the outcomes are not interchangeable. Some are event counts, while others describe duration, and each captures a different part of the clinical course.

The posted secondary results include comparisons of ICU admission, ICU days, and days of hospitalization. Their estimates do not all carry the same level of precision, and the registry record does not report analyses for the full set of secondary outcomes. The secondary pattern should be read as supporting context for the primary result rather than as a separate resolution of uncertainty about mortality. The primary endpoint remains the prespecified outcome identified in the record; secondary results do not replace it.

There are 14 outcome measures in the registry record, and 13 secondary outcomes are posted. When multiple outcomes are examined, some differences can arise by chance even if there is no underlying effect. This is why unadjusted secondary findings generally carry less confirmatory weight than a primary comparison, especially when the registry record does not document a multiplicity adjustment, hierarchy, or analysis plan.

The registry record does not report which secondary outcomes were treated as confirmatory, how missing values were handled, or whether analyses were adjusted for baseline factors. No analysis-specific results are reported for the listed secondary comparisons. These gaps limit how strongly the secondary outcomes can be used to corroborate or challenge the primary result. Their role is descriptive and hypothesis-generating unless additional prespecified analysis details are available.

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

• Number of Participants Admitted to the ICU
• Days of Stay in the Intensive Care Unit
• Days of Hospitalization
• Number of Participants That Required Higher Levels of Oxygen Supplementation
• Number of Participants That Required Invasive Mechanical Ventilation
• Duration of Invasive Mechanical Ventilation
• Number of Participants That Required ECMO
• Number of Participants That Required Tracheostomy

9. Statistical Interpretation

10. Statistical Methods Explained

The outcome is binary at the participant level: each participant either met the mortality endpoint by 28 days or did not. For a binary outcome, a group risk is the proportion of participants with the event. The posted proportions are 0.208 for standard-dose dexamethasone and 0.171 for weight-based dexamethasone. The risk difference compares those proportions by subtracting the standard-dose risk from the weight-based risk. Its negative estimate, -0.037, indicates a lower observed risk in the weight-based group in this sample, while uncertainty around that estimate remains substantial.

What does the risk difference express?

The risk difference is an absolute contrast on the risk scale, rather than a relative comparison. Its interpretation depends on the order of groups: the posted estimate compares weight-based dose with standard dose. A value below zero means the observed event risk was lower in the weight-based group; a value above zero would mean it was higher. The estimate is not a causal conclusion by itself. Randomization supports a fair comparison in principle, but the uncertainty interval and the trial’s conduct and analysis details also matter.

How should the interval be read?

An interval around an estimate describes statistical uncertainty under the method used to construct it. In general, a wider interval indicates less precision than a narrower interval. The interval for the primary risk difference ranges from -0.166 to 0.092, spanning negative and positive values and including zero. The confidence level and the specific interval-construction method are not reported in the registry record. It is therefore best to describe the reported bounds without assigning a confidence level that the record does not state.

What does the p-value add?

The unadjusted p-value is 0.575. In general, a p-value measures how unusual results at least as discrepant as those observed would be under a specified statistical model in which there is no group difference. It does not measure the probability that the treatment has no effect, and it does not measure the probability that the finding is due to chance. It also does not convey the size or clinical importance of an effect. The estimate and interval are needed to understand the direction and range of plausible effects.

Why are recalculated results described as unadjusted?

The posted comparisons are recalculated from group-level summary statistics and are not an adjusted analysis. An adjusted analysis might account for prespecified participant characteristics or other model terms, but the registry record does not report such a primary analysis or the covariates it would use. A calculation from aggregate counts also cannot reproduce an undocumented participant-level model. The discrepancy indicator is false, so there is no recorded discrepancy requiring the sponsor’s own analysis to take precedence over these recalculations.

Why does randomization not remove all uncertainty?

Random assignment is intended to make groups comparable, on average, with respect to factors that may affect outcomes. It does not guarantee that the groups are identical in a particular trial. With limited participant counts and relatively few primary events, the estimate can remain imprecise. Randomization also does not settle questions about missing data, adherence, outcome ascertainment, or analysis choices; those depend on trial conduct and reporting. The registry record does not report enough detail to evaluate each of those issues fully.

Why can the secondary comparisons be more fragile?

Several secondary outcomes were posted, covering ICU admission and duration, hospitalization, oxygen supplementation, invasive ventilation, ECMO, and tracheostomy. Looking across many outcomes creates multiple opportunities for an apparently unusual result. General statistical practice treats unadjusted secondary comparisons as exploratory unless the analysis plan and multiplicity strategy support stronger confirmatory interpretation. The registry record does not report a multiplicity strategy or analysis-specific results. The secondary estimates should therefore be considered alongside the primary outcome, not as independent proof of a treatment effect.

Why do event counts and averages require different summaries?

For a binary outcome, the relevant summaries are counts, group risks, and a contrast such as a risk difference. For continuous outcomes such as duration, the registry posts means and standard deviations. A mean describes the arithmetic average, while a standard deviation describes variation among observations around that average. These summaries answer different questions and should not be combined as if they were the same type of endpoint. A comparison of means can also be affected by skewed distributions or influential observations; the registry record does not report distributional checks or the underlying participant-level data.

In general, over-dispersion matters when observed variability exceeds what a statistical model assumes. That can make standard errors too small and intervals too narrow if it is ignored. Whether over-dispersion is relevant depends on the outcome and model; the registry record does not report an outcome model or diagnostics for the primary endpoint. No claim about a particular model assumption can therefore be made from the record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.037, with reported bounds from -0.166 to 0.092. The interval is broad enough to include zero and values on both sides of zero. That pattern indicates that the direction of the mortality difference is not determined precisely by the posted results. The point estimate alone should not be treated as the settled effect.

In general, an interval expresses uncertainty about an estimate under a statistical method. An interval that includes zero does not prove there is no effect, just as an interval that excludes zero would not by itself establish clinical importance. The interval’s confidence level and construction method are not reported in the registry record, so the bounds can be quoted but should not be assigned an unreported confidence level.

The trial’s posted group sizes were 72 and 70, and the observed primary event counts were 15 and 12. Event counts and participant counts affect the precision of a binary-outcome estimate; sparse information generally limits how tightly an effect can be estimated. The registry’s interval reflects uncertainty from the recalculated unadjusted comparison, not uncertainty about every possible source of bias or variation in future settings.

Precision is distinct from clinical relevance. The interval spans effects that could matter in either direction, but the registry record does not define a threshold for a clinically important difference. It also does not provide a prespecified equivalence or non-inferiority margin. The result therefore cannot be interpreted as proving equivalence or ruling out meaningful effects.

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 sample-size table and curve are planning illustrations based on the observed effect, not the trial’s original design assumptions. Every displayed sample-size figure is participants per arm; the calculation is not a total number of events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is expressed as the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect, if the planning assumptions and statistical model hold. The 90% power column gives the corresponding planning target for a 90% chance. These are design probabilities under assumed conditions, not guarantees about what a future trial will find. They do not say how likely the observed result in this completed trial was to occur.

The rows distinguish planning for 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so detecting a smaller effect requires more participants under the same assumptions. The displayed values are therefore scenarios rather than a single recommended target. Because they are derived from an observed effect, they are sensitive to the uncertainty in that effect estimate.

This is not observed power. Observed power calculated from the trial’s result would not add useful information beyond the estimate and its uncertainty; the displayed figures instead illustrate future sample-size requirements under explicit planning assumptions.

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 = 0.208; treatment proportion p₁ = 0.171; average p̄ = 0.190.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5547 = 1.0871.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5540 = 0.4663.
4. n = (1.0871 + 0.4663)² / (-0.0369)² = 1,771.8, rounded up to 1,772 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 <- 0.208333333333333                          # control proportion
p1 <- 0.171428571428571                          # 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(4834375)
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 = 1,772 (80% power), 2,372 (90% power)
 75% of observed effect: n per arm = 3,209 (80% power), 4,296 (90% power)
 50% of observed effect: n per arm = 7,351 (80% power), 9,840 (90% power)
power.prop.test: 1771.8 
Simulated power at n = 1,772 per arm: 0.803 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study assesses several outcomes, subgroups, time points, or statistical contrasts. The more comparisons made, the greater the chance that at least one may appear unusual by chance. General statistical approaches can address this through a prespecified hierarchy or adjustment, but the appropriate approach depends on the study’s aims and analysis plan. The registry record lists 14 outcome measures and reports 13 secondary outcomes, but does not report a multiplicity strategy. The unadjusted secondary comparisons should therefore not be treated as if they were protected against multiple testing.

The record does not report how missing outcome data were handled, whether any participants were excluded from an analysis, or how incomplete follow-up was addressed. This absence of reporting does not establish that data were missing, nor does it establish that there were no missing data. It means the impact of missingness cannot be evaluated from the registry record alone.

The registry record also does not identify a primary analysis population, such as an intention-to-treat or per-protocol population, or state how participants were analyzed if treatment was discontinued or not followed as assigned. Randomization is part of the design, but the analysis population and handling of deviations are needed to understand how the randomized comparison was carried through in the analysis.

No interim analyses or stopping rules are reported in the registry record. The original statistical plan, including any prespecified model or covariate adjustment, is also not reported. These details matter because decisions made during a trial and choices among analytical approaches can affect how results should be interpreted. Their absence from the record limits assessment; it is not evidence that any particular procedure was used or omitted.

15. 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 0% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event record lists serious adverse events in 0 participants in the standard-dose group, among 72 at risk, and 0 participants in the weight-based group, among 70 at risk. This means no serious adverse events are recorded in these entries. It does not establish that no safety events of any kind occurred, and it should not be read as a comprehensive assessment of safety beyond the registry’s reported data.

Other adverse events were recorded for 24 participants in the standard-dose group and 13 in the weight-based group. The adverse-event record also lists 17 deaths and 12 deaths, respectively. Those death entries should not be substituted for the primary endpoint counts of 15 and 12: the primary endpoint is mortality at 28 days, whereas the registry comment says participants were followed to the end of admission for final disposition.

The record does not provide detailed event terms for serious events, and the list of top serious-event terms is empty. The adverse-event figures are descriptive and do not, on their own, establish a comparative safety effect. Differences in reporting, follow-up, and outcome definitions also matter when interpreting these counts.

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

The posted primary results show 15 deaths among 72 participants assigned standard-dose dexamethasone and 12 among 70 assigned weight-based dexamethasone by 28 days. The unadjusted risk-difference estimate favors the weight-based group numerically, but its interval includes zero and extends in both directions. The result therefore leaves uncertainty about whether, and by how much, mortality differed between groups.

These data do not establish that the higher dose improves outcomes. They also do not establish that it worsens outcomes or that the two dosing strategies are equivalent. Establishing equivalence would require an appropriate design and a prespecified margin, neither of which is reported in the registry record. A non-significant p-value is not evidence that the treatments are identical.

The secondary outcomes may add context about care and illness course, but they are numerous and the registry record does not report a multiplicity plan. They should not be used to turn an uncertain primary result into a definitive conclusion. Likewise, the planning illustrations are not evidence that the completed trial had a particular probability of detecting an effect.

The result applies to this randomized, open-label comparison and its recorded 28-day endpoint. The registry does not report enough detail to assess all eligibility criteria, missing-data handling, analysis populations, or adjustment choices. Those limitations constrain generalization and interpretation. The record also distinguishes 28-day mortality from final disposition at the end of admission, so those counts answer different questions.

In short, the trial offers a randomized comparison with a negative point estimate for the weight-based versus standard-dose risk difference, but substantial uncertainty remains. The posted numbers describe what was observed; they do not by themselves determine the effect of either dose in other populations or settings.

17. Why This Trial Matters Statistically

This trial is statistically instructive because the point estimate and the uncertainty tell different parts of the story. The estimate is negative, indicating fewer observed 28-day deaths in the weight-based group in this sample. Its interval, however, covers zero and values in either direction. Reporting the point estimate alone would obscure the uncertainty; reporting only the p-value would obscure both the effect scale and the range of compatible values.

The randomized design provides a useful framework for comparing the dose strategies, while the absence of masking and the limited detail in the registry record leave important questions about conduct and analysis. Randomization is not a substitute for transparent reporting of analysis populations, missing data, and prespecified methods. Those details are especially important when interpreting outcomes beyond the primary endpoint.

The record also illustrates why secondary outcomes need careful interpretation. Clinical trials may measure multiple aspects of illness, but repeated unadjusted comparisons can produce findings that look persuasive by chance. A broad set of outcomes can be useful for generating hypotheses, yet it cannot replace a clear primary analysis and a documented approach to multiplicity.

Finally, planning illustrations derived from an observed effect should not be mistaken for the original trial’s sample-size rationale or for observed power. They show how assumed effect sizes relate to future planning under stated assumptions. Keeping that distinction clear helps prevent estimates from being treated as more definitive than the data support.

18. Limitations

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

The trial was open-label, with no masking recorded. Awareness of assigned dose can potentially affect care decisions, co-interventions, or outcome assessment, depending on the setting and outcome. All-cause mortality is less subjective than many outcomes, but open-label design remains relevant to secondary measures such as admission, oxygen support, and duration of care. The registry record does not describe procedures to limit such influences.

The primary estimate is based on the posted group counts of 72 and 70, with 15 and 12 events. Its interval is wide and includes zero, leaving considerable uncertainty about the size and direction of a difference. The record does not report a prespecified threshold for a clinically important effect, nor an equivalence or non-inferiority margin.

Several details needed to evaluate internal validity are not reported in the registry record: the original sample-size justification, detailed eligibility criteria, analysis population, missing-data handling, and adjusted analysis plan. The registry record also does not report interim analyses or a multiplicity strategy. These are reporting limitations; they should not be mistaken for evidence that a specific method was or was not used.

Follow-up definitions require care. The primary outcome is mortality at 28 days, while the registry comment describes follow-up through the end of admission for final disposition. Death counts recorded for those different windows are not interchangeable. The posted secondary outcomes cover different kinds of measures, and the available record does not provide analysis-specific results for the complete outcome set. These factors limit the strength of conclusions that can be drawn from the registry record alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Randomized Open Investigation Determining Steroid Dose — NCT04834375.
• Registry record last updated 2023-07-20; status last verified 2023-07.
• Results first posted 2023-07-20.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed phase 3 randomized, open-label, parallel-group trial sponsored by Northwell Health. It enrolled 142 participants and compared standard dexamethasone, 6 mg intravenously daily for 10 days, with weight-based dexamethasone, 0.2 mg/kg/day intravenously up to 20 mg daily for 10 days.

The primary endpoint was all-cause mortality at 28 days. The posted counts were 15 of 72 in the standard-dose group and 12 of 70 in the weight-based group. The recalculated unadjusted risk difference was -0.037, with an interval from -0.166 to 0.092 and an unadjusted p-value of 0.575. The interval includes zero, so the estimate remains uncertain.

The registry lists multiple secondary outcomes and adverse-event counts. It does not report the original sample-size justification, a detailed statistical analysis plan, missing-data handling, analysis populations, or a multiplicity strategy. The record distinguishes 28-day mortality from final disposition at the end of admission.