Vitamin D to Improve Outcomes by Leveraging Early Treatment: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Vitamin D to Improve Outcomes by Leveraging Early Treatment (NCT03096314), a randomized phase 3 study. The primary outcome is All-cause, All-location Mortality to Day 90.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group trial with quadruple masking. The registry record identifies Massachusetts General Hospital as the sponsor and reports an enrollment of 1358. The study status is completed. The listed start date is 2017-04-27, and the primary completion date is 2018-12-11.

The comparison was a single enteral dose of high-dose vitamin D3 against a matched placebo. The brief summary says randomization occurred within 12 hours after the decision to admit a patient to an intensive care unit. It also describes treatment as an early intervention, with the assigned dose administered within 2 hours of randomization according to the arm descriptions. The brief summary characterizes the trial as double-blind; the design fields identify quadruple masking.

The primary outcome was all-cause, all-location mortality to day 90, with vital status determined through medical record review, calls to patients or proxies or healthcare facilities, obituary review, or information from the Centers for Disease Control and Prevention's National Death Index. The primary analysis population was limited to subjects whose vitamin D deficiency was confirmed by LC/MS/MS testing. The treatment-arm counts used for that primary result were 531 for high-dose vitamin D and 528 for placebo. These analysis counts need not equal the overall enrollment, because they describe the reported primary analysis population rather than everyone enrolled.

Secondary outcomes included mortality at day 28, hospital mortality by day 90, being alive and home at the prior level of care at day 90, lengths of stay, ventilator-free days, health-related quality of life by EQ-5D-5L, and new ARDS by day 7. The registry record lists 22 outcome measures and 27 analyses. Further details about allocation procedures, the original sample-size justification, and the planned statistical analysis are 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: After initial study screening, eligible patients were consented and received secondary screening for vitamin D deficiency; performed via an FDA-approved test (either hospital clinical laboratory or the FastPack IP device (Qualigen Inc., Carlsbad, CA). Participants with a screening 25OHD level \<20 ng/mL were randomized for treatment assignment.

Screened Vitamin D Deficient

Reasons for not completing this period:

Confirmed Vitamin D Deficient

Analysis population for the primary outcome, as defined in the registry: The primary analysis included subjects who had confirmed vitamin D deficiency by LC/MS/MS testing.

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.

Population: There were 1360 patients who screened as vitamin D deficient (all randomized) and received a confirmatory LC/MS/MS test (liquid chromatography tandem mass spectrometry). Subjects with a 25OHD result \<20 ng/L by LC/MS/MS were the confirmed deficient cohort and included in the primary analysis (N= 538 in Vit D Arm and N = 540 in Placebo arm).

6. Primary Endpoint

The registry lists the primary outcome as All-cause, All-location Mortality to Day 90, measured over 90 days after randomization.

The primary endpoint counts participants who died from any cause, in any location, by 90 days after randomization. It is a binary outcome at the participant level: each person is classified according to whether death occurred within the specified follow-up period. The registry record describes several ways of establishing vital status, including medical records, calls, obituary review, and the National Death Index.

All-cause mortality is a broad endpoint because it does not depend on assigning a particular cause of death. Including all locations also means that the outcome is not restricted to deaths occurring in the hospital. These features make the endpoint directly interpretable as whether a participant was alive at the specified time, while avoiding reliance on a narrower cause-specific classification.

The primary analysis was restricted to participants with vitamin D deficiency confirmed by LC/MS/MS testing. This distinction matters: the primary result describes that analysis population, not necessarily every enrolled participant. The endpoint is a count of participants with an event, and the treatment comparison is presented as a risk difference, with the registry's own analysis reported as a superiority analysis.

Although the endpoint is clinically meaningful, a count at a fixed follow-up time does not describe when deaths occurred during follow-up. Nor does it, by itself, establish the reason for any difference in counts. Interpretation therefore depends on the comparison between groups, the uncertainty around that comparison, and the analysis methods reported in the registry record.

7. Results Posted in the Registry

• High Dose Vitamin D Formulation: 23.5% (125/531) versus 20.6% (109/528) on control; risk difference 2.9 percentage points (95% CI -2.1 to 7.9), risk ratio 1.14 (0.91–1.43); unadjusted two-proportion z-test p = 0.256.

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.

All-cause, All Location Mortality to Day 28

• 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:
  • High Dose Vitamin D Formulation: 17.3% (92/531) versus 13.1% (69/528) on control; risk difference 4.3 percentage points (95% CI -0.1 to 8.6), risk ratio 1.33 (0.99–1.77); unadjusted two-proportion z-test p = 0.054.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High Dose Vitamin D Formulation and the control. The interval gives the range of effects that remain compatible with the data.

Hospital Mortality to Day 90

• 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:
  • High Dose Vitamin D Formulation: 17.1% (92/538) versus 13.4% (72/539) on control; risk difference 3.7 percentage points (95% CI -0.5 to 8.0), risk ratio 1.28 (0.96–1.70); unadjusted two-proportion z-test p = 0.087.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High Dose Vitamin D Formulation and the control. The interval gives the range of effects that remain compatible with the data.

Alive and Home (Prior Level of Care) at Day 90

• 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:
  • High Dose Vitamin D Formulation: 65.9% (348/528) versus 65.6% (345/526) on control; risk difference 0.3 percentage points (95% CI -5.4 to 6.0), risk ratio 1.00 (0.92–1.10); unadjusted two-proportion z-test p = 0.913.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High Dose Vitamin D Formulation and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span mortality at a shorter follow-up, hospital mortality, being alive and home at the prior level of care, lengths of stay, ventilator-free days, health-related quality of life, and new ARDS. The registry record lists 21 posted secondary outcomes. Together, they broaden the clinical description beyond the primary mortality endpoint, but they do not form a single unified measure of treatment effect.

The posted results do not establish a consistent secondary pattern that changes the interpretation of the primary analysis. Each outcome has its own definition, follow-up period, and analysis population, and the denominators vary across outcomes. The secondary findings should therefore be read as additional observations rather than as a substitute for the prespecified primary comparison. Their relationship to the primary result is contextual: they can describe other dimensions of outcomes, but they do not resolve the uncertainty in 90-day all-cause, all-location mortality.

Unadjusted secondary results carry less weight because examining many outcomes increases the chance that some comparisons appear notable even when there is no underlying effect. In general, multiplicity procedures can control that risk, but whether such procedures were planned or used is not reported in the registry record. The record also does not establish which secondary outcomes were prespecified in the final analysis plan or how missing observations were handled. Without those details, individual secondary findings should be treated cautiously and not elevated above the primary result.

These limitations do not make secondary outcomes irrelevant. They can reveal whether the broad pattern of results is coherent and identify questions that might merit further study. But interpretation should account for the number of comparisons, their varying populations, and the uncertainty of each estimate. The registry record does not report a formal method for combining the secondary outcomes into an overall conclusion.

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

• All-cause, All Location Mortality to Day 28
• Hospital Mortality to Day 90
• Alive and Home (Prior Level of Care) at Day 90
• Hospital Length of Stay to Day 90
• Healthcare Facility Length of Stay to Day 90
• Ventilator-free Days (VFDs) to Day 28
• Health-related Quality of Life by EuroQol (EQ-5D-5L)
• Number of Participants Who Developed (New) ARDS to Day 7

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either had the event by the specified time or did not. The posted arm counts and the comparison are therefore interpreted as event counts and proportions, with the main contrast expressed as a risk difference. Statistical methods help distinguish the observed difference in these trial groups from the uncertainty that remains about the underlying group difference.

What does a risk difference express?

A risk difference compares the proportion with an event in one group with the proportion in the other group by subtracting one group's proportion from the other's. A value of zero corresponds to equal event proportions. Positive or negative values indicate direction according to the order of groups used in the comparison. For the primary recalculation, the posted risk difference is 0.029, where the comparison is high-dose vitamin D against placebo. This is an unadjusted estimate derived from the posted summary counts.

The registry record reports the sponsor's primary analysis as a generalized linear model and gives p = 0.26. The record does not specify the model link, covariates, or additional details needed to reproduce that analysis. The recalculated estimate and p-value are consequently best understood as a straightforward, unadjusted comparison, rather than as an attempt to duplicate the sponsor's model.

What does a confidence interval contribute?

A confidence interval describes uncertainty in an estimated effect. In general, a wider interval indicates less precision, while a narrower one indicates greater precision. For the primary recalculation, the interval ranges from -0.021 to 0.079 and includes zero. This means the data do not sharply distinguish the estimate from no difference, and the interval also permits effects in either direction. A confidence interval is not a guarantee that the true effect lies within its endpoints, and it does not show the probability that a particular effect is true.

How should a p-value be read?

In general, a p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not quantify the chance that the result is due to chance in a general sense. The sponsor-reported p-value of 0.26 is not conventionally small evidence against the null hypothesis of no group difference. The unadjusted recalculation gives p = 0.256. These values should be interpreted in light of the different descriptions of the analyses; the registry's model-based result is the reported sponsor analysis.

What do relative measures add?

The recalculated comparison also includes a risk ratio and an odds ratio. In general, a risk ratio compares event proportions as a ratio, whereas an odds ratio compares event odds. Both are relative measures; the risk difference is an absolute measure on the proportion scale. Relative measures can look different from an absolute difference because they use different scales. They should not be compared as if they were interchangeable, and neither scale removes uncertainty from the estimate.

For the primary outcome, the posted recalculated risk ratio is 1.14, with an interval from 0.909 to 1.431; the odds ratio is 1.184, with an interval from 0.885 to 1.583. Each interval includes the corresponding null value for its measure. These are unadjusted recalculations from posted summary statistics, not the sponsor's generalized linear model output.

Why distinguish analysis populations?

The registry record specifies that the primary analysis included subjects with vitamin D deficiency confirmed by LC/MS/MS testing. The primary arm counts are 531 and 528, while the overall enrollment is 1358. These are different quantities: enrollment describes the trial, whereas the arm counts describe participants included in the stated primary outcome analysis. The record does not fully explain the flow from enrollment to each analysis population, so reasons for differences in denominators are not reported in the registry record.

For binary outcomes, denominators matter because event counts cannot be interpreted without knowing how many participants contributed to the comparison. Secondary outcomes use different group counts, which may reflect outcome-specific availability or definitions; the reasons are not reported in the registry record. No further assumptions about missing observations or exclusions should be inferred from the counts alone.

Why can over-dispersion matter?

Over-dispersion is a general concern when outcome variation exceeds what a statistical model assumes. It can make standard errors too small if not appropriately addressed, leading to confidence intervals that are too narrow or p-values that are too small. This trial's primary outcome is binary, and the registry record identifies a generalized linear model, but it does not provide enough model detail to assess whether over-dispersion was relevant or how it was handled. No conclusion about that issue can be drawn from the available record.

In general, randomization supports a fair comparison of assigned groups, but it does not eliminate uncertainty, guarantee complete outcome data, or explain every feature of the analysis. The record describes quadruple masking and the randomized parallel-group design; details about concealment procedures, model specification, covariate adjustment, and prespecified analysis decisions are not reported in the registry record.

11. Confidence Intervals and Precision

The primary event counts are 125 of 531 participants in the high-dose vitamin D group and 109 of 528 in the placebo group. The recalculated risk difference is 0.029, and its confidence interval ranges from -0.021 to 0.079. Because the interval spans zero, the posted summary data are compatible with no difference as well as with effects in either direction. The interval is not narrow enough to support a precise conclusion about the magnitude of the difference.

In general, a confidence interval captures the range of effect estimates that are reasonably compatible with the data and the assumptions of the method used. It reflects sampling uncertainty, but does not account for every possible source of bias or uncertainty in trial conduct. The recalculated interval is unadjusted; the registry's sponsor analysis reports p = 0.26 but does not give a confidence interval for the primary result in the reported analysis.

Precision is also distinct from statistical significance. A result that does not meet a conventional significance threshold may still leave meaningful effects plausible, especially when the interval is broad. Conversely, an estimate near zero does not prove that the true difference is exactly zero. The primary evidence should therefore be read as uncertain rather than as establishing equivalence.

The secondary outcomes also have intervals for some comparisons, but their interpretation is affected by the number and variety of outcomes. Interval estimates from unadjusted analyses do not automatically provide family-wise protection against false-positive findings. In addition, the registry record does not report whether secondary analyses were adjusted or how missing data were handled. Those limitations affect how confidently the numerical precision can be translated into broader conclusions.

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 estimates are planning illustrations based on the observed effect, not the trial's original design assumptions. For these binary outcomes, the figures are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The trial's own original sample-size justification and assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under its assumptions. The 90% power column uses a higher chance of detecting that same effect and therefore generally requires more participants per arm. These are planning quantities, not counts of participants who experienced an outcome.

The estimates are shown for planning at 100%, 75%, and 50% of the observed effect. Smaller effects require more participants to distinguish them from no difference with a given power and significance level. This is why the planning figures increase as the target effect becomes a smaller fraction of the observed estimate. When the observed effect is small or uncertain, the resulting planning estimates can be very large and should not be read as a recommendation for a future trial without other design considerations.

These figures are not observed power. Observed power is not a useful substitute for interpreting the uncertainty in the result; the effect estimate and its confidence interval describe the posted evidence more directly. The planning illustrations instead answer a prospective question under their stated assumptions: how many participants per arm might be needed to detect an effect of a chosen size. They do not show how likely the trial's actual result was to occur or prove that a result has an effect of the assumed size.

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 = 0.206; treatment proportion p₁ = 0.235; average p̄ = 0.221.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5867 = 1.1499.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5864 = 0.4935.
4. n = (1.1499 + 0.4935)² / (0.0290)² = 3,219.1, rounded up to 3,220 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 <- 0.206439393939394                          # control proportion
p1 <- 0.235404896421846                          # 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(3096314)
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 = 3,220 (80% power), 4,309 (90% power)
 75% of observed effect: n per arm = 5,657 (80% power), 7,572 (90% power)
 50% of observed effect: n per arm = 12,574 (80% power), 16,832 (90% power)
power.prop.test: 3219.1 
Simulated power at n = 3,220 per arm: 0.801 (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

The registry's reported primary analysis is a generalized linear model, with a superiority analysis and p = 0.26. The simple recalculation from the posted primary counts gives a risk difference of 0.029, with an unadjusted p-value of 0.256. No discrepancy is identified between the recalculation and the sponsor's reported analysis.

The recalculation is not a reconstruction of the generalized linear model. It uses only the posted event counts and denominators, without additional adjustment. The registry record does not provide the model specification, covariates, or enough details to reproduce the sponsor's analysis. The sponsor's result is therefore the appropriate account of the analysis actually reported by the trial registry; the recalculation is a supplementary, unadjusted check based on aggregate counts.

The registry record does not provide a sponsor-reported confidence interval or effect estimate for the primary comparison in the reported analysis. The interval attached to the recalculation should not be attributed to the sponsor. Both sets of results are consistent in not presenting strong evidence of a primary group difference, but their analytic bases are not identical. Any apparent similarity should not be taken to mean that the model-based analysis has been independently reproduced.

15. Multiplicity, Missing Data and Analysis Populations

The record lists 22 outcome measures, 27 analyses, and 21 posted secondary outcomes in addition to the primary endpoint. Testing multiple outcomes can increase the chance of at least one apparently unusual result, even when each individual test uses a conventional significance threshold. In general, multiplicity adjustments or a prespecified hierarchy of outcomes can address some of this concern. Whether the trial used such an approach, and which outcomes were included in any adjustment, are not reported in the registry record.

The primary analysis population is described as subjects with vitamin D deficiency confirmed by LC/MS/MS testing. That is useful information about who contributed to the primary analysis, but it is not a complete account of participant flow or missing data. The record does not report how many participants had missing day-90 vital status, whether any outcome data were imputed, or what rules were used for exclusions from each analysis. It also does not report a full intention-to-treat or per-protocol analysis definition.

The endpoint description indicates that vital status could be determined through several sources, including medical records, calls, obituary review, and the National Death Index. The methods used to establish status are described, but the record does not provide the amount of missingness or explain how unresolved status was handled. The primary outcome counts should therefore be interpreted within the stated confirmed-deficiency analysis population, without assuming that every enrolled participant contributed to that result.

For secondary outcomes, the denominators vary. The registry record does not explain the reasons for those differences or report a comprehensive missing-data strategy for all outcomes. In general, missingness can affect estimates if the likelihood of having an observed outcome is related to the outcome itself or to group assignment. That is a general statistical concern, not a claim about what occurred in this trial.

The record also does not report the original statistical analysis plan, interim analyses, stopping rules, or the rationale for the planned enrollment. These items should not be inferred from the posted results or the planning illustrations. Their absence limits assessment of whether every analysis followed a prespecified plan and how all sources of uncertainty were considered.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: death (0.3%), readmission (0.3%), altered mental status (0.1%), blindness (0.1%), breathing kussmaul type (0.1%).

The safety listing reports 14 participants with serious adverse events among 690 at risk in the high-dose vitamin D group and 18 among 668 at risk in the placebo group. These are the serious-event figures in the safety record; they are separate from the primary analysis counts and should be interpreted using their stated safety denominators. The record also lists deaths as 159 in the high-dose vitamin D group and 137 in the placebo group within its adverse-event data. Those figures should not be substituted for the primary day-90 mortality comparison, which uses its own endpoint definition and analysis population.

The most frequent serious adverse-event terms listed are Death and Readmission, each at 0.3%; Altered Mental Status, Blindness, Breathing Kussmaul Type, and Cardiac Arrest are each listed at 0.1%. These are registry-reported percentages. The record does not provide further detail in the posted listing to establish causes, timing, severity beyond the serious-event classification, or how individual events were attributed.

Safety counts describe reported events in the listed groups. They do not by themselves establish that an assignment caused an event or provide a complete comparative safety analysis. Differences in the safety denominators and the method of collecting or classifying events should be considered, but additional details are not reported in the registry record.

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

The primary result describes a comparison of 90-day all-cause, all-location mortality among participants whose vitamin D deficiency was confirmed by LC/MS/MS testing. The posted counts are 125 of 531 for high-dose vitamin D and 109 of 528 for placebo. The registry's generalized linear model analysis reports p = 0.26; the recalculated unadjusted risk difference is 0.029, with an interval that includes zero. Taken together, these results do not provide strong statistical evidence of a difference in the primary outcome.

That interpretation does not mean the groups have been proven identical. The recalculated interval allows a range of plausible effects, and the registry record does not report a sponsor confidence interval for its model-based primary result. A lack of conventionally strong statistical evidence is not the same as evidence that no effect exists. Nor does the point estimate alone establish a difference that is certain, clinically important, or caused by the assigned treatment.

The primary finding applies to the stated analysis population, outcome definition, and follow-up period. It does not automatically apply to every critically ill patient, to people without confirmed deficiency, or to outcomes that were not measured. The trial compared early administration of a single dose of vitamin D3 with placebo; it does not, from the posted data alone, answer questions about other dosing schedules or treatment strategies.

Secondary and safety results provide additional context, but they do not replace the primary comparison. Their number, differing denominators, and uncertainty limit how firmly they can support broad conclusions, especially where multiplicity and missing-data methods are not reported. The statistical reading is therefore limited to what the registry record documents: an inconclusive primary comparison and additional outcomes that require cautious interpretation. It is not medical advice.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can produce a clear endpoint definition and still leave meaningful uncertainty about the effect. The primary outcome is easy to interpret at the participant level—death from any cause, in any location, by day 90—but the statistical conclusion depends on both the estimated contrast and its precision. The posted analysis does not provide strong evidence of a primary difference, while the recalculated interval remains broad enough to include effects in either direction.

The trial also highlights why analysis populations and denominators matter. Overall enrollment is 1358, while the primary result uses participants with vitamin D deficiency confirmed by LC/MS/MS testing. Secondary and safety analyses use different counts. These distinctions are important for readers who might otherwise assume that every posted statistic describes the same participants and outcome definition.

There is also a useful distinction between the sponsor's model-based analysis and an unadjusted recalculation from summary counts. The recalculation can make the comparison transparent and provide a check on the reported result, but it cannot reproduce undocumented modeling choices. Statistical interpretation should preserve that distinction rather than treating every estimate as interchangeable.

Finally, the many outcomes underscore the importance of prespecification and multiplicity. A broad set of measures can provide a richer description of trial outcomes, but isolated secondary results require caution when the analysis plan and multiplicity procedures are not reported. The record's limitations do not erase the trial's contribution; they define the boundaries within which its posted results can be interpreted.

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 primary result is reported for participants with vitamin D deficiency confirmed by LC/MS/MS testing, and the record does not provide a complete account of how the 1358 enrolled participants flowed into that analysis population. The reasons that the primary arm counts differ from overall enrollment are not reported in the registry record. This limits independent assessment of exclusions, missing outcomes, and the extent to which the result represents all randomized participants.

The registry record describes a generalized linear model for the primary analysis but does not report the model specification, link function, covariates, or confidence interval for the sponsor's primary estimate. The unadjusted recalculation from summary counts is informative but cannot address any adjustments used in the model. The record also does not report the original sample-size justification, the planned analysis details, or whether any interim analyses took place.

Several secondary outcomes were posted, with varying denominators and outcome definitions. The record does not explain all denominator differences, give a complete account of missing-data handling, or state whether multiplicity was controlled. As a result, secondary findings have limited ability to provide confirmatory evidence beyond the primary outcome.

The safety listing gives event counts and selected serious-event terms, but the registry record does not provide detailed timing, adjudication procedures, or attribution for those events. The counts should not be interpreted as causal comparisons without those details. More generally, the results describe the trial population and the specified single-dose intervention; the record does not establish how results would apply to different populations, regimens, or clinical settings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Vitamin D to Improve Outcomes by Leveraging Early Treatment — NCT03096314.
• Registry record last updated 2020-01-27; status last verified 2020-01.
• Results first posted 2020-01-27.
• 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 record describes a completed, randomized, quadruple-masked, parallel-group phase 3 trial sponsored by Massachusetts General Hospital, with enrollment of 1358. It compared a single enteral dose of 540,000 IU vitamin D3 with matched placebo in critically ill patients screened for vitamin D deficiency. The primary endpoint was all-cause, all-location mortality 90 days after randomization, analyzed in subjects with deficiency confirmed by LC/MS/MS testing.

The primary counts were 125 of 531 in the high-dose group and 109 of 528 in the placebo group. The registry reports a generalized linear model analysis with p = 0.26. An unadjusted recalculation gives a risk difference of 0.029 and a confidence interval that includes zero. The primary comparison is therefore statistically inconclusive, rather than proof of equality or of a treatment effect.

The record lists a broad set of secondary outcomes and adverse-event information. Interpretation is limited by unreported details about the original sample-size rationale, full analysis plan, missing data, and multiplicity. Secondary and safety findings should be read in that context.