Magnesium Sulfate vs Placebo for Placental Abruption: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Magnesium Sulfate vs Placebo for Placental Abruption (NCT00186069), a randomized na study. The primary outcome is Undelivered With Resolution of Vaginal Bleeding and Contractions in First 48 Hours.

2. Clinical Question

The registry describes the study as evaluating the safety and efficacy of magnesium sulfate for preterm suspected abruption. Its primary endpoint combines being undelivered at the specified time with resolution of both vaginal bleeding and uterine contractions. It is therefore a joint clinical status, not a measure of bleeding alone, contraction relief alone, or time to delivery.

The registry reports 12 participants with the outcome in the magnesium sulfate group and 10 in the normal saline group, with 15 participants listed in each group. These counts describe the posted primary outcome; they do not by themselves establish whether the difference is compatible with chance or how precisely the underlying group outcomes are estimated. The statistical comparisons and their uncertainty need to be considered alongside the counts.

3. Trial Design

This is a randomized, double-blind study comparing magnesium sulfate with normal saline. The registry lists the study as completed, with an enrollment of 30. It identifies Stanford University as the sponsor. The record gives a start date of 2004-03 and a primary completion date of 2014-06. These dates describe the registry record and do not by themselves explain the length of recruitment or follow-up.

The intervention descriptions list a 4 gram bolus followed by 2 grams per hour for both magnesium sulfate and normal saline. The record does not explain the rationale for these regimens or provide further information about how treatment was administered, adherence, or other aspects of trial conduct. The stated objective concerns safety and efficacy for preterm suspected abruption.

There is an inconsistency in the design fields: the allocation is listed as randomized, two intervention groups and their outcome counts are reported, but the model field says single-group. The registry does not clarify this mismatch. It is therefore appropriate to describe the reported randomized, two-group comparison while noting that the model classification is internally inconsistent.

The primary endpoint is a binary participant outcome assessed 48 hours after randomization. The registry also names gestational age at delivery and neonatal Apgar score at 5 minutes as secondary outcomes. The record does not report detailed eligibility criteria, the method used to conceal allocation, the sequence-generation procedure, or the planned analysis population. The original sample-size assumptions and the rationale for the enrollment target 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.

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 Undelivered With Resolution of Vaginal Bleeding and Contractions in First 48 Hours, measured over 48 hours after the randomization.

The primary endpoint counts participants who were undelivered at 48 hours after randomization and whose vaginal bleeding and uterine contractions had resolved. A participant must meet all parts of that definition to count as having the outcome. The registry describes the measure as a proportion, while the posted group results give participant counts: 12 for magnesium sulfate and 10 for normal saline, with 15 participants listed in each group.

This kind of combined endpoint can summarize whether several clinically relevant conditions are present at a specified time. It is not equivalent to measuring each component separately. For example, the record does not give separate outcome counts for resolution of bleeding, resolution of contractions, or remaining undelivered. Nor does it describe how resolution was assessed or whether assessment was standardized.

A fixed-time binary outcome is often straightforward to compare between groups because each participant is classified as having or not having the specified outcome by the assessment time. That clarity depends on a consistent definition and complete ascertainment. The registry does not report details about endpoint assessment, missing observations, or how participants with incomplete status at 48 hours were handled.

The endpoint is not a time-to-event measure: it records status at the stated assessment time rather than the exact time when symptoms resolved or delivery occurred. The registry names gestational age at delivery and neonatal Apgar score at 5 minutes as secondary outcomes, but their results are not reported in the record.

7. Results Posted in the Registry

• Normal Saline: 66.7% (10/15) versus 80.0% (12/15) on control; risk difference -13.3 percentage points (95% CI -44.6 to 18.0), risk ratio 0.83 (0.54–1.29); unadjusted two-proportion z-test p = 0.409.

8. Statistical Interpretation

9. Statistical Methods Explained

The outcome is binary: each participant either met the combined endpoint by 48 hours or did not. For each group, the registry reports the number meeting the endpoint and the group size. A group proportion expresses the count with the outcome relative to the number assessed in that group. These proportions are the building blocks for comparing groups, but the registry’s primary results are counts rather than a detailed account of every participant’s outcome status.

What does a risk difference express?

A risk difference subtracts one group’s event proportion from the other group’s event proportion. It is expressed on an absolute scale, so it describes the difference in the proportion of participants meeting the endpoint. The re-calculation is expressed as normal saline minus magnesium sulfate, producing -0.133. A negative estimate in that ordering means the observed proportion was lower in the normal saline group. The confidence interval from -0.446 to 0.179 includes zero, the value corresponding to no absolute difference. Because the interval spans values on both sides of zero, the estimated direction is uncertain.

How do risk ratios and odds ratios differ?

A risk ratio compares the outcome proportions in two groups by division. A value of one corresponds to equal proportions; values on either side indicate a relative difference, with interpretation depending on which group is in the numerator. The re-calculated risk ratio is 0.833 for normal saline relative to magnesium sulfate. The odds ratio instead compares the odds of the outcome between groups. Odds are not the same as proportions, and an odds ratio can look different in magnitude from a risk ratio. The re-calculated odds ratio is 0.5. These measures answer related but distinct questions; they are not competing estimates of the same scale.

What is Fisher’s exact test?

The sponsor’s reported analysis identifies Fisher Exact as its method and reports a risk ratio of 1.20, a 95% confidence interval from 0.77 to 1.86, and p = 0.68. Fisher’s exact test is a method for assessing evidence of association in a two-by-two table, with calculations based on the possible arrangements of the observed counts under a null model. It is commonly useful when group counts are small. The registry does not provide further detail about the exact procedure used to obtain the sponsor’s risk-ratio interval or whether any additional analysis choices were applied.

The simple re-calculation gives an unadjusted p-value of 0.409 and estimates the risk difference, risk ratio, and odds ratio directly from the posted group summaries. It is not an adjusted model and does not account for participant-level covariates. The sponsor’s result is a separate reported analysis, using its stated test and group ordering. A difference between p-values can arise from differences in the statistical methods and the quantity being tested; p-values from different procedures should not be compared as if they were repeated measurements of one fixed quantity.

What do p-values and confidence intervals tell readers?

A p-value summarizes how compatible the observed data are with a specified null hypothesis under the assumptions of the chosen test. It does not quantify the size of an effect, the probability that a treatment is beneficial, or the probability that the null hypothesis is true. A confidence interval gives a range of estimates compatible with the data and method at its stated confidence level. General statistical interpretation treats the interval as a guide to both plausible effect sizes and precision, not as a range guaranteed to contain the true effect in an individual study.

For a risk difference, zero is the no-difference value; for a ratio measure, one is the no-difference value. Both the sponsor’s interval and the re-calculated intervals include their relevant no-difference value. That observation does not prove that the groups are identical. It indicates that the estimates remain uncertain under the analyses reported.

Why does small-sample analysis require care?

With limited counts, conventional approximations can be less reliable, and exact methods can be useful for testing. Regardless of method, small data sets generally offer limited information about the range of effects compatible with the observations. The reported interval widths make that uncertainty visible. General statistical practice also distinguishes a test of a null hypothesis from estimation: the point estimate describes the observed contrast, while the interval shows its uncertainty under the method.

The registry lists randomization and double masking, but it does not report enough methodological detail to assess sequence generation, allocation concealment, masking procedures, analysis population, or handling of missing data. The statistical results should therefore be read as the analyses documented in the record, rather than as evidence that unreported design or analysis procedures were used.

10. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is located, not whether its direction is favorable. The re-calculated risk difference is -0.133, with a confidence interval from -0.446 to 0.179. This interval extends from a sizeable negative difference to a positive difference. Since zero lies within it, the data do not sharply distinguish a difference in either direction from no absolute difference under this method.

The alternative re-calculated measures show the same general uncertainty. The risk ratio for normal saline relative to magnesium sulfate is 0.833, with an interval from 0.538 to 1.292. The odds ratio is 0.5, with an interval from 0.095 to 2.628. A ratio interval that includes one is compatible with no relative difference; these intervals also encompass materially different relative effects. The different scales should not be compared by their numerical widths.

The sponsor reports a risk ratio of 1.20 with a 95% confidence interval from 0.77 to 1.86. That interval also includes one. Its breadth means that the reported estimate does not pin down the relative effect precisely. The sponsor’s confidence interval is based on its stated analysis, whereas the recalculated intervals are unadjusted estimates from the posted summaries.

Confidence intervals are not guarantees about the true effect. In general, an interval procedure is designed to have its stated coverage across repeated studies under its assumptions. Here, the modest group counts and broad intervals mean that the observed data leave substantial uncertainty. The record does not report a precision target or an original sample-size rationale, so it cannot establish whether the study was designed to estimate the endpoint with a particular degree of precision.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect and the stated assumptions: two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The calculations consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the number of participants per arm indicated by the planning calculation for an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were true. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are prospective planning concepts, not probabilities that the observed result is correct. The figures are 172 and 230 participants per arm for planning around 100% of the observed effect; 294 and 392 for 75% of the observed effect; and 631 and 844 for 50% of the observed effect.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more participants under the same assumptions. The planning exercise is anchored to this study’s observed effect, which is uncertain; it should not be treated as a reliable estimate of the effect a future study will observe. The numbers are not observed power. They do not tell whether the completed study had a particular probability of detecting its true effect.

The original enrollment was 30, with 15 participants listed in each group. Those observed group sizes are distinct from the larger prospective planning illustrations. The registry does not explain whether its original target was based on a different effect, a safety objective, practical constraints, or another design consideration.

12. 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 = 0.800; treatment proportion p₁ = 0.667; average p̄ = 0.733.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6254 = 1.2257.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6182 = 0.5203.
4. n = (1.2257 + 0.5203)² / (-0.1333)² = 171.5, rounded up to 172 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 <- 0.8                          # control proportion
p1 <- 0.666666666666667                          # 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(186069)
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 = 172 (80% power), 230 (90% power)
 75% of observed effect: n per arm = 294 (80% power), 392 (90% power)
 50% of observed effect: n per arm = 631 (80% power), 844 (90% power)
power.prop.test: 171.5 
Simulated power at n = 172 per arm: 0.806 (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.

13. Analyses Reported by the Sponsor

The sponsor’s posted primary analysis reports a risk ratio of 1.20 for magnesium sulfate relative to normal saline, with a 95% confidence interval from 0.77 to 1.86 and p = 0.68. The analysis names Fisher Exact as the method. The re-calculation uses the group counts and reports the risk difference, risk ratio, odds ratio, and an unadjusted p-value. Its risk ratio is oriented as normal saline relative to magnesium sulfate, so its direction is reversed compared with the sponsor’s ordering.

The sponsor’s estimate of 1.20 matches the ratio implied by the posted group proportions when magnesium sulfate is the numerator. The re-calculated ratio is the corresponding comparison in the opposite direction. The sponsor’s p-value and the re-calculated p-value are not identical because the procedures differ. The record does not provide enough detail to reconstruct every aspect of the sponsor’s calculation.

The discrepancy flag is false. The sponsor’s result should therefore be presented as the registry’s reported analysis, alongside—not replaced by—the simple unadjusted re-calculation. Both the sponsor interval and the re-calculated intervals include the no-difference value appropriate to their measure. Neither analysis yields a narrow estimate. The reported result and the re-calculation should be understood as analyses of the same posted group outcome, not as independent replications.

14. Multiplicity, Missing Data and Analysis Populations

The registry names gestational age at delivery and neonatal Apgar score at 5 minutes as secondary outcomes, in addition to the primary outcome. Results for those secondary outcomes are not reported in the registry record. Without their estimates and uncertainty, they cannot be used to extend the interpretation of the primary result.

When a study examines multiple outcomes or multiple comparisons, the chance of obtaining at least one apparently unusual result can increase if each is assessed separately at a conventional threshold. Statistical approaches to multiplicity can address that issue, but the appropriate approach depends on the prespecified questions and analysis plan. The registry record does not report whether multiplicity adjustments were planned or applied, how outcomes were prioritized beyond identifying the primary outcome, or whether additional analyses were conducted. No multiplicity strategy should be inferred from the posted analysis alone.

Missing-data handling is also not reported. The group sizes and endpoint counts are posted, but the record does not explain whether all randomized participants had endpoint status assessed, how any missing 48-hour information was treated, or whether the analysis followed an intention-to-treat approach. It does not describe exclusions from the analysis or give a participant flow account. These omissions limit assessment of whether the reported counts represent all randomized participants as intended.

The record identifies randomized allocation and double masking, but the analysis population and details of the randomization process are not reported. It also does not describe adjustments for baseline characteristics, sensitivity analyses, interim analyses, or the statistical plan in enough detail to assess these practices. Their absence from the registry record is not evidence that they were or were not performed. It means the documented primary result should be interpreted without assuming unreported procedures.

15. 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 5% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures list zero serious events among 15 participants at risk in the magnesium sulfate group and zero among 15 participants at risk in the normal saline group. No serious adverse event terms are listed. The deaths field is not reported in the registry record.

The registry also lists other adverse events affecting 2 participants in the magnesium sulfate group and 3 participants in the normal saline group, with 15 participants at risk in each group. These are presented separately from serious adverse events. The record does not provide event terms, severity details, timing, or additional information needed to assess the nature of these other events.

Zero recorded serious events in these groups means that none are listed in the registry’s serious-event counts; it does not establish that the risk of serious events is absent. With limited group sizes, uncommon harms may not be observed. The safety figures are descriptive and should not be treated as a precise comparison of safety between groups. The registry record does not report a broader safety analysis or additional detail about adverse-event collection.

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

The posted primary outcome shows 12 participants meeting the combined endpoint in the magnesium sulfate group and 10 in the normal saline group, with 15 listed in each group. The sponsor’s analysis reports a risk ratio of 1.20 for magnesium sulfate relative to normal saline, with a 95% confidence interval from 0.77 to 1.86 and p = 0.68. The unadjusted re-calculation expresses the contrast in several ways and likewise has broad uncertainty intervals that include the no-difference value.

These results describe the observed data and do not establish a precise difference between the groups. An interval that includes no difference is not proof that the treatments have identical outcomes, just as the point estimate alone is not proof of a real difference. The data remain compatible with a range of effects in either direction under the reported methods.

The endpoint concerns a particular combined status at 48 hours after randomization. It does not separately establish what happened to bleeding, contractions, or delivery timing, and it is not a substitute for the named secondary outcomes. Results for gestational age at delivery and neonatal Apgar score at 5 minutes are not reported in the registry record.

The findings are specific to the study population and conduct described in the record, which gives limited eligibility and analysis detail. The record describes preterm suspected abruption but does not provide a fuller population profile. These statistics do not establish effects in other settings or populations, and they do not provide medical advice. Their main statistical message is that the observed group counts are accompanied by substantial uncertainty.

17. Why This Trial Matters Statistically

This study illustrates why a result should be read through both its estimate and its uncertainty. The observed counts differ, but the group sizes are limited and the confidence intervals cover values on both sides of no difference. Focusing only on which group has the larger count would omit the uncertainty that is central to interpreting a small trial.

It also illustrates that the same outcome can be described on multiple statistical scales. A risk difference expresses an absolute contrast, while risk ratios and odds ratios express relative contrasts. Group ordering matters: reversing the numerator and denominator changes the direction of a ratio. Reporting the measure, comparison order, interval, and test helps prevent a numerical result from being interpreted in the wrong direction.

The sponsor’s reported Fisher Exact analysis and the unadjusted re-calculation produce different p-values. That is a useful reminder that methods matter, particularly with limited counts. A p-value is not a stand-alone verdict, and differences between tests do not mean that the underlying observed counts have changed. The estimates and their intervals give readers more information about possible effect sizes and precision.

The study also has a registry model classification that conflicts with its randomized, two-group reporting. Noting such inconsistencies, and distinguishing reported details from unreported design details, is part of careful evidence assessment. The planning illustrations further show how detecting smaller effects generally requires larger samples, while remaining separate from the study’s original design rationale and from any claim about observed power.

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 registry record gives limited detail for evaluating the trial’s conduct and analysis. Although it lists randomized allocation and double masking, it does not report the sequence-generation method, allocation concealment, details of masking, eligibility criteria, participant characteristics, or the analysis population. The model field says single-group despite the randomized allocation and the two reported groups; the registry does not resolve this inconsistency.

The primary outcome combines being undelivered with resolution of bleeding and contractions at a fixed time. Separate component results and details of outcome assessment are not reported. Missing-data handling, participant flow, treatment adherence, and exclusions are also not described. These gaps make it difficult to assess how completely the endpoint was ascertained and whether the posted counts represent the intended analysis population.

The record names two secondary outcomes but does not report their results. It does not describe a multiplicity strategy, a detailed statistical analysis plan, interim analyses, adjusted analyses, or sensitivity analyses. The original sample-size rationale and design assumptions are not reported; the planning illustrations based on the observed effect do not supply that missing rationale.

The adverse-event record lists serious-event counts and other-event counts but lacks event terms and further clinical detail. The deaths field is not reported. Finally, the reported group sizes are limited, and the estimates have broad intervals. These limitations constrain precision and the depth of interpretation; they do not by themselves determine the direction or validity of the underlying treatment effect.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Magnesium Sulfate vs Placebo for Placental Abruption — NCT00186069.
• Registry record last updated 2018-01-02; status last verified 2017-12.
• Results first posted 2017-04-20.
• 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 describes a completed randomized, double-blind study of magnesium sulfate versus normal saline for preterm suspected placental abruption, sponsored by Stanford University. Enrollment is listed as 30. The record gives a start date of 2004-03 and a primary completion date of 2014-06.

The primary outcome is the number of participants undelivered at 48 hours after randomization with resolution of vaginal bleeding and uterine contractions. The posted counts are 12 of 15 for magnesium sulfate and 10 of 15 for normal saline. The sponsor reports a risk ratio of 1.20, a 95% confidence interval from 0.77 to 1.86, and p = 0.68 using Fisher Exact. The unadjusted re-calculation also indicates substantial uncertainty.

Gestational age at delivery and neonatal Apgar score at 5 minutes are named secondary outcomes, but their results are not reported. Serious adverse event counts are zero in both groups; other adverse events are listed for 2 and 3 participants, respectively. The record does not provide a detailed account of missing data, analysis populations, or the original sample-size rationale.