Effect of Vitamin D3 Supplementation in Pregnancy on Risk of Pre-eclampsia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Vitamin D3 Supplementation in Pregnancy on Risk of Pre-eclampsia (NCT03101150), a randomized phase 1, phase 2 study. The primary outcome is Number of Participants With Pre-eclampsia in Both Arms.

2. Clinical Question

The trial record describes a comparison of two supplementation regimens among pregnant participants selected for vitamin D deficiency. It does not describe a comparison with placebo or no supplementation: both groups received vitamin D3, with one receiving it as part of an antenatal multivitamin and the other as drops. The clinical question is therefore about the contrast between these recorded daily doses under the trial conditions, rather than the effect of supplementation against no supplementation.

The principal outcome was a count of participants with pre-eclampsia in each group. The registry description says the event was assessed irrespective of vitamin D dose. This makes the outcome a binary event measure at the participant level: each participant either had a recorded event or did not. The record also lists change in vitamin D level and intrauterine growth retardation as secondary outcomes. These outcomes can add context to the trial record, but they do not replace the primary question, and their interpretation depends on the analyses and reporting available for each.

The record identifies the trial as completed and gives an enrollment of 179. Outcome denominators are reported separately for the two groups and are not identical to the enrollment figure. Participant flow and the reasons for any difference between enrollment and outcome denominators are not reported in the registry record. Accordingly, the estimates describe the posted outcome counts and should not be treated as a complete account of every participant’s follow-up.

3. Trial Design

NCT03101150 is listed as a randomized, parallel-group trial with no masking. Its phase is recorded as phase 1 and phase 2. The sponsor is King Fahad Medical City. The registry record lists the start date as 2012-10-01, the primary completion date as 2014-10-31, and the status as completed. Enrollment is recorded as 179.

The two groups received different daily vitamin D3 regimens. The 400 IU group received vitamin D3 contained in an antenatal multivitamin once daily by mouth, beginning at 14 weeks of pregnancy and continuing till delivery. The 4000 IU group received vitamin D3 drops once daily by mouth over the same stated period. Both arms therefore involve supplementation; the comparator is the lower-dose regimen rather than an untreated group.

Random allocation is relevant because, in principle, it aims to create groups that are comparable at the start of a trial. The registry record does not report the allocation sequence method, whether allocation was concealed, or any stratification factors. Because masking is listed as none, the study is open label according to the record. Details about which people knew the assigned regimen and whether outcome assessment was independent or masked are not reported in the registry record.

The registry describes an outcome comparison of pre-eclampsia cases and lists two secondary outcomes: change in vitamin D level and the number of patients with intrauterine growth retardation. The primary outcome timeframe is described as from 20 weeks of pregnancy until pre-eclampsia or assessment up to 32 weeks, whichever came first. The other outcome timeframes are at the 36th week of pregnancy and at delivery, respectively. A more detailed protocol, a statistical analysis plan, participant flow, and the original sample-size justification are not reported in the registry record. The recorded phase, allocation, masking, and outcome summaries define the design information available for statistical interpretation; they do not establish details beyond what the registry states.

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: 416 participants were screened. 192 did not meet eligibility criteria. 38 refused to participate and 7 turned out to be ectopic pregnancy.

Overall Study

Reasons for not completing this period:

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 With Pre-eclampsia in Both Arms, measured over From 20 weeks of pregnancy till event of pre-eclampsia seen, whichever came first, assessed up to 32 weeks..

The primary endpoint is the number of participants with pre-eclampsia in each arm. The registry describes occurrence as yes or no for each participant, assessed from 20 weeks of pregnancy until the event or assessment up to 32 weeks, whichever came first. This is a binary outcome summarized as a count, with the number of participants in each arm providing the denominator for interpretation.

A binary event endpoint is useful when the clinical question concerns whether a defined event occurred during a specified period. Counts alone do not convey how common the event was in each group, so they need to be read alongside each arm’s outcome denominator. The posted results report 6 of 81 participants in the 400 IU arm and 1 of 83 in the 4000 IU arm. Those are the observed counts and denominators in the registry outcome record; they are not the enrollment total.

The event count is not a time-to-event analysis. The registry does not post event times or a survival analysis for this outcome. It also does not describe adjudication procedures or additional diagnostic criteria for pre-eclampsia. Those details are not reported in the registry record. Thus, the endpoint can be interpreted as the registry’s recorded binary comparison over the stated timeframe, while the extent of information about event definitions and follow-up completeness remains limited.

Pre-eclampsia is the primary outcome because it is the event named in the trial’s central comparison and the primary outcome listing. A primary endpoint helps focus interpretation, but it does not by itself resolve uncertainty in the estimate, differences between the sponsor analysis and a simple re-calculation, or the limitations of the available reporting.

7. Results Posted in the Registry

• 4000 IU: 1.2% (1/83) versus 7.4% (6/81) on control; risk difference -6.2 percentage points (95% CI -12.4 to -0.0), risk ratio 0.16 (0.02–1.32); unadjusted two-proportion z-test p = 0.049.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change in Vitamin D Level

• 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:
  • 4000 IU: mean 72.30 versus 35.30 on control; difference 37.00 (95% CI 28.97 to 45.03), standardized effect d = 1.40; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for 4000 IU than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Patients With Intrauterine Growth Retardation

• 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:
  • 4000 IU: 9.6% (8/83) versus 22.2% (18/81) on control; risk difference -12.6 percentage points (95% CI -23.6 to -1.5), risk ratio 0.43 (0.20–0.94); unadjusted two-proportion z-test p = 0.027.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for 4000 IU than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The two posted secondary outcomes cover different kinds of information: a continuous measurement of vitamin D level and a binary count of participants with intrauterine growth retardation. Their overall pattern is that the higher-dose arm has a higher vitamin D level at the stated assessment time and fewer recorded intrauterine growth retardation cases at delivery. These outcomes offer supporting context about the trial’s recorded measurements, but they do not answer the primary question about pre-eclampsia directly.

The secondary results are directionally consistent with the primary event-count pattern in that the group receiving 4000 IU has the more favorable numerical result for each of the posted outcomes. Directional consistency across endpoints does not establish a common causal mechanism, prove that one result explains another, or resolve the uncertainty in the primary estimate. The outcomes have different measurement scales and timeframes, and the record does not report an analysis linking changes in vitamin D level to either clinical outcome.

The registry reports unadjusted secondary analyses. When several outcomes are examined, the chance of obtaining at least one apparently notable result can increase, depending on the analysis plan and the relationship among outcomes. No multiplicity adjustment, hierarchy for interpreting secondary outcomes, or prespecified strategy for combining them is reported in the registry record. For that reason, unadjusted secondary results generally carry less confirmatory weight than a clearly prespecified primary analysis.

There are two secondary outcomes posted in the record, and both are reported with comparisons between the same groups. The registry does not explain whether other outcomes were planned but omitted, whether analyses were conducted on all randomized participants, or how missing measurements were handled. The secondary findings are best read as descriptive and supportive evidence within the limits of the recorded analyses. They should not be used to override the primary result or its uncertainty.

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

• Change in Vitamin D Level
• Number of Patients With Intrauterine Growth Retardation

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods help translate outcome counts into estimates of the contrast between groups and show how uncertain those estimates are. The registry reports a chi-squared method for its primary binary outcome and gives a risk ratio, confidence interval, and p-value. A separate simple, unadjusted re-calculation from the posted counts expresses the contrast as a risk difference. These are distinct effect measures, so their values answer related but not identical questions.

What does a risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the comparison group. A value below zero in the posted orientation means the event proportion is lower in the 4000 IU arm than in the 400 IU arm. The re-calculated estimate is -0.062. Its confidence interval lies below zero but approaches zero closely. This measure expresses an absolute contrast in proportions. It does not describe how many events would occur in a different population, and it should not be interpreted independently of the observed counts, denominators, and uncertainty interval.

What does a risk ratio describe?

A risk ratio compares the event proportion in one group with the event proportion in the other. A ratio of 1 is the null value, indicating equal proportions under the measure. Values below 1 indicate a lower observed proportion in the numerator group relative to the reference group; values above 1 indicate a higher proportion. The sponsor reports a risk ratio of 0.163 and a 95% confidence interval from 0.02 to 1.32. Since that interval extends across 1, it includes the null value for this measure. The registry also reports p <0.05 for that analysis. The tension between the interval and p-value should be retained in interpretation, rather than resolved by choosing one and ignoring the other.

What is a confidence interval?

A confidence interval gives a range of effect estimates compatible with the data under the method used, with the stated confidence level. It describes precision as well as direction: a narrower interval indicates greater precision, whereas a wider interval indicates more uncertainty. It is not a range containing a fixed proportion of individual participant outcomes, nor does it assign a probability that the true effect lies in the particular interval after the data have been observed. Here, the sponsor’s primary risk-ratio interval includes the null value, while the re-calculated risk-difference interval is close to the null boundary. The two intervals should not be compared as though they were on the same scale.

How should a p-value be read?

A p-value is calculated under a specified statistical model and a null hypothesis. It describes how unusual data at least as incompatible with that null would be if the null and model assumptions held. It is not the probability that the null is true, the probability that chance alone caused the findings, or a measure of clinical importance. The registry’s primary p-value is reported as p <0.05, and the simple re-calculation is 0.049. A result close to a conventional threshold does not create a sharp boundary between strong and weak evidence. The confidence interval, effect measure, event counts, analysis method, and reporting consistency all matter.

Why can analyses differ?

Risk difference and risk ratio use different scales and can produce different interval behavior. Statistical procedures may also differ in their treatment of sparse counts and variance. The registry states that the reported method was chi-squared, but the record does not provide enough detail to establish all implementation choices or to reproduce the sponsor’s analysis. The sponsor’s reported risk ratio is not the same calculation as the unadjusted risk difference from the posted counts. The discrepancy flag means the sponsor’s own analysis takes precedence. Recalculation is informative as a check on the posted summaries, but it is not a substitute for the trial’s reported analysis.

What does randomization contribute?

Randomization is intended to reduce systematic differences between treatment groups at allocation, thereby supporting a fair comparison. It does not guarantee that all baseline characteristics are identical in a particular trial, and it does not address bias that can arise after allocation through missing outcomes, deviations from assigned treatment, or outcome assessment. The record identifies randomized allocation and no masking, but allocation concealment, baseline characteristics, adherence, and analysis-population details are not reported in the registry record. These unknowns limit assessment of how fully the intended protections were implemented.

Why does outcome sparsity matter?

When an outcome is uncommon and the number of events is small, effect estimates and uncertainty can be sensitive to individual observations. General statistical reasoning therefore gives particular weight to the interval and to the exact event counts, rather than relying only on a threshold label for a p-value. Sparse data can also make the performance of approximate methods more dependent on assumptions. The registry names a chi-squared analysis, but does not report a method comparison or a sensitivity analysis for sparse outcomes.

The primary outcome is reported as a binary count, not as a continuous measurement or a time-to-event endpoint. The statistical methods and interpretation should match that structure. A risk difference describes an absolute group contrast, a risk ratio describes a relative contrast, and neither removes uncertainty about the underlying effect or limitations in the registry’s reporting.

11. Confidence Intervals and Precision

Precision concerns how narrowly an effect is estimated. The primary outcome is based on 6 events in the 400 IU group and 1 event in the 4000 IU group, with denominators of 81 and 83. The re-calculated risk difference is -0.062, and its confidence interval lies below zero but approaches it closely. That proximity means the interval permits estimates close to no difference, so the numerical direction should not be mistaken for a highly precise estimate.

The sponsor’s primary reported risk ratio is 0.163, with a 95% confidence interval from 0.02 to 1.32. This interval is broad and spans the null value of 1. It therefore conveys uncertainty across interpretations that include a lower relative event proportion and no difference, as well as values on the other side of the null. The sponsor’s reported p <0.05 does not erase that interval information. The inconsistency between the interval and p-value is a feature of the registry record that should remain visible in statistical interpretation.

Confidence intervals are not guarantees about the effect, and their width depends on the observed information and the method used. The comparatively small event counts mean the primary estimate has limited information behind it. More generally, the confidence interval concerns compatibility with the analysis assumptions; it does not account for every source of uncertainty, such as unreported participant flow or missing-data handling.

The outcome denominators differ from the enrollment figure of 179, and the record does not state why. Without participant flow and missing-data details, it is not possible to determine whether the reported confidence intervals reflect all randomized participants or how missing outcomes were treated. The registry also does not report adjusted estimates. The intervals consequently quantify statistical uncertainty under the reported or re-calculated methods, not uncertainty from every design and reporting limitation.

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 figures are planning illustrations based on observed effects, not the trial’s original design calculations. For the non-time-to-event outcomes in this record, the figures are participants per arm, not total participants or total events. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the illustrative number of participants per arm required for an analysis to have an 80% chance of detecting the stated effect if that effect and the calculation assumptions were correct. The 90% power column uses a higher target chance of detection and therefore calls for more participants per arm. These are planning concepts, not guarantees for a particular future study. They depend on assumptions about the effect, allocation, significance level, and analysis method.

For the primary outcome, planning for 100% of the observed effect corresponds to 167 participants per arm for 80% power and 224 participants per arm for 90% power. Planning for 75% of the observed effect corresponds to 349 and 467 participants per arm, respectively. Planning for 50% of the observed effect corresponds to 899 and 1,203 participants per arm, respectively. Smaller effects require more participants because they are harder to distinguish from random variation.

These illustrations use the observed effect as a starting point, which is uncertain, especially when based on few events. They do not establish what the original investigators expected, what their original target was, or whether the completed trial was adequately powered. The trial’s own sample-size justification and design assumptions are not reported in the registry record. This is not observed power: the figures are prospective planning calculations, not a measure of the probability that the completed trial detected its true effect.

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 = 0.074; treatment proportion p₁ = 0.012; average p̄ = 0.043.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2871 = 0.5627.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2837 = 0.2388.
4. n = (0.5627 + 0.2388)² / (-0.0620)² = 167.0, rounded up to 167 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 <- 0.0740740740740741                          # control proportion
p1 <- 0.0120481927710843                          # 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(3101150)
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 = 167 (80% power), 224 (90% power)
 75% of observed effect: n per arm = 349 (80% power), 467 (90% power)
 50% of observed effect: n per arm = 899 (80% power), 1,203 (90% power)
power.prop.test: 167 
Simulated power at n = 167 per arm: 0.843 (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 reports the sponsor’s primary analysis as a chi-squared comparison expressed as a risk ratio of 0.163, with a 95% confidence interval from 0.02 to 1.32 and p <0.05. The simple unadjusted re-calculation from the posted counts instead reports a risk difference of -0.062 and an unadjusted p-value of 0.049. A risk ratio and a risk difference are different effect measures, so their numerical values cannot be compared directly. Both summarize the contrast between the same posted groups, but on different scales.

The record flags a discrepancy. Under the stated interpretation of that flag, the sponsor’s own analysis takes precedence over the simple re-calculation. The re-calculation remains a useful transparent check based on the posted counts, but it should not be presented as correcting or replacing the sponsor’s analysis. There is also an internal tension within the sponsor’s reported primary results: the confidence interval includes 1, the null value for a risk ratio, while its p-value is reported 0.05.

The registry does not provide sufficient detail to explain the discrepancy or reconcile the reported interval and p-value. The reported method is named, but further calculation details and a full statistical analysis plan are not reported in the registry record. Interpretation should therefore retain the sponsor’s result as the trial’s reported analysis, identify the interval-p-value inconsistency, and treat the unadjusted re-calculation as a distinct analysis of the posted summary counts.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when more than one outcome, comparison, subgroup, or analysis is examined. Even if each analysis uses a conventional significance threshold, conducting multiple analyses can raise the chance that at least one result appears statistically notable by chance. This is a general statistical consideration; it does not establish that any particular result in this trial is spurious.

The registry lists one primary outcome and two secondary outcomes. It does not report a multiplicity adjustment, a testing hierarchy, or a statistical analysis plan describing how the primary and secondary findings were to be interpreted together. It is therefore not possible to determine from the registry record whether the reported p-values were adjusted, whether the primary endpoint was protected as the sole confirmatory test, or whether the secondary outcomes were intended as exploratory. The secondary analyses should consequently be read with more caution than a prespecified primary analysis.

Missing-data handling is also not described in sufficient detail. The enrollment figure is 179, whereas the posted primary outcome denominators are 81 and 83. Secondary outcome denominators are also reported as 81 and 83. The adverse-event groups use different at-risk denominators. The registry does not explain these differences, give a participant disposition account, or state whether missing measurements were excluded, imputed, or handled by another method. No assumptions about missingness or sensitivity analyses for missing data are reported.

The analysis population is not specified in the posted results. The record does not say whether the outcome analyses followed an intention-to-treat approach, included participants according to treatment received, or used another population definition. It does not provide adherence information or describe protocol deviations. These omissions matter because the analysis population and missing-data approach can influence estimates in a randomized trial, especially when outcome counts are sparse.

The registry also does not report details such as allocation concealment, baseline balance, or whether outcome assessment was independent of treatment assignment. The record identifies no masking. These details are relevant to assessing the risk of bias but cannot be inferred from the listed trial design. Together, the missing multiplicity, missing-data, and analysis-population information limits how completely the statistical evidence can be evaluated.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The adverse-event record lists 86 participants at risk in the 400 IU group and 93 in the 4000 IU group. It records 0 participants affected by serious adverse events and 0 affected by other adverse events in each group. These are the reported figures for the adverse-event entries; they should be read with their at-risk denominators and not assumed to have the same denominator as the primary outcome analysis.

The record does not list serious adverse-event terms. Death counts are recorded as null rather than as a numeric count, so deaths are not reported in the registry record. The adverse-event entries do not provide event descriptions, timing, severity grading beyond the serious-versus-other categories, or a detailed account of collection and follow-up procedures. The difference between the adverse-event at-risk denominators and the primary outcome denominators is not explained.

Zero recorded affected participants is a statement about the posted entries, not proof that no events occurred outside the recorded definitions, reporting period, or captured population. The registry information is therefore limited for comparing safety experiences. These figures describe what the record lists and do not support a broader conclusion about safety.

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

The posted counts show fewer recorded pre-eclampsia events in the 4000 IU group than in the 400 IU group. The simple unadjusted risk-difference estimate is negative, and its interval is close to zero at one end. The sponsor’s analysis reports a risk ratio below 1, but its confidence interval includes 1 while its p-value is reported 0.05. These results describe the observed data and the uncertainty attached to the analyses; they do not provide a single unambiguous statistical message.

The randomized design is relevant to interpreting a group comparison, but the registry record alone does not establish every element needed to assess bias or applicability. The record identifies vitamin D deficient pregnant participants and the two supplementation regimens, but it does not provide detailed eligibility criteria, baseline characteristics, adherence, participant flow, or the analysis population. The outcome denominators are smaller than the enrollment figure, and the handling of missing outcomes is not reported. These limitations qualify how broadly the estimates can be interpreted.

The results do not establish that the higher dose caused the observed differences, nor do they establish that the doses are equivalent. A confidence interval that includes a null value does not prove no effect, and a p-value below a conventional threshold does not prove that an effect is important or reliable. The primary sponsor analysis has an interval-p-value tension, and the record flags a discrepancy between the posted analysis and simple re-calculation. The sponsor’s analysis takes precedence, while the re-calculation provides a separate view of the summary counts.

The secondary outcomes provide additional measurements but are unadjusted and not reported with a multiplicity plan. They should be treated as supportive rather than definitive. The safety entries show zero affected participants in the posted categories, but deaths are not reported and the safety denominators differ from the outcome denominators. Taken together, the record gives a description of observed group differences with important statistical and reporting uncertainty. It does not justify medical advice or a treatment recommendation.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its primary outcome is binary and relatively sparse in the posted data. The contrast between 6 events in one group and 1 in the other produces a directionally clear difference in the counts, but the small event totals make the estimate sensitive to individual observations. Reading the interval alongside the point estimate helps keep the observed direction distinct from the precision of the estimate.

It also illustrates how effect measures frame a result differently. The re-calculated risk difference describes an absolute contrast, whereas the sponsor reports a relative comparison as a risk ratio. Those quantities should not be substituted for one another. In addition, the sponsor’s reported confidence interval and p-value do not tell a fully consistent story about the null value. The record’s discrepancy flag is a reminder that a re-calculation can be informative without superseding the trial’s reported analysis.

The design information also matters. This was a randomized, open-label, parallel-group comparison of two active supplementation regimens, not supplementation against no supplementation. That distinction defines the question the trial can address. The registry names the main outcome timeframe and reports two secondary outcomes, but leaves the original sample-size rationale, participant flow, missing-data methods, analysis population, and multiplicity strategy unreported.

Finally, planning calculations based on observed effects demonstrate why the assumed effect size strongly influences illustrative sample-size requirements. Smaller target effects require more participants per arm under the listed planning assumptions. These calculations are not evidence of the trial’s original planning or observed power. Collectively, the record is useful for teaching the separation of design, effect size, uncertainty, analysis reporting, and confirmatory interpretation.

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 specific to this trial follow from the available registry record. The primary outcome is based on few recorded events, and the risk-ratio confidence interval reported by the sponsor includes the null value despite a reported p-value below 0.05. The record flags a discrepancy, but does not explain its source. The sponsor’s analysis takes precedence, while the unadjusted re-calculation from the posted counts should remain a separate, supplementary calculation.

The outcome denominators do not match the enrollment figure, and participant flow is not reported. The record does not explain exclusions, losses to follow-up, or how missing primary and secondary outcomes were handled. Analysis population and treatment adherence are also not described. These omissions make it difficult to assess whether the posted groups and analyses reflect all randomized participants as intended.

The trial is listed as having no masking. Further details about outcome assessment and allocation concealment are not reported. The registry does not give a detailed diagnostic definition or adjudication process for pre-eclampsia, nor does it report baseline characteristics that would help assess the realized balance of randomized groups. These details should not be assumed.

The secondary findings are reported without a stated multiplicity approach, and the original sample-size justification is not reported. The planning illustrations use observed effects and therefore cannot establish whether the trial was originally designed around a clinically relevant target or whether its enrollment was adequate for that purpose. The adverse-event denominators differ from the primary outcome denominators; deaths are not reported, and detailed safety collection procedures are absent.

Generalizability is also constrained by the population description available in the registry, which identifies vitamin D deficient pregnant participants but does not state how deficiency was defined or provide further eligibility information. The trial compares two active vitamin D3 regimens and cannot, from this comparison alone, describe the effect of supplementation versus no supplementation. These limits concern the record’s scope and detail, not proof that the underlying study lacked procedures that are simply unreported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of Vitamin D3 Supplementation in Pregnancy on Risk of Pre-eclampsia — NCT03101150.
• Registry record last updated 2018-11-02; status last verified 2018-02.
• Results first posted 2018-11-02.
• 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

NCT03101150 is a completed randomized, open-label, parallel-group phase 1 and phase 2 trial sponsored by King Fahad Medical City. Enrollment is recorded as 179. The study compared daily 400 IU vitamin D3 in an antenatal multivitamin with daily 4000 IU vitamin D3 drops among pregnant participants described as vitamin D deficient.

The primary endpoint was the number of participants with pre-eclampsia. The registry reports 6 of 81 in the 400 IU group and 1 of 83 in the 4000 IU group. The sponsor reports a chi-squared risk-ratio analysis with a 95% confidence interval that includes the null and p <0.05; the record flags a discrepancy, so the sponsor analysis takes precedence over the simple unadjusted re-calculation.

Two secondary outcomes are posted, along with adverse-event entries. Important details, including participant flow, missing-data methods, analysis population, multiplicity handling, and the original sample-size justification, are not reported in the registry record. The posted results should be interpreted as estimates with uncertainty and reporting limitations, not as medical advice.