Moxibustion in a Randomized Trial for Version of Breech Position From Week 32: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Moxibustion in a Randomized Trial for Version of Breech Position From Week 32 (NCT02251886), a randomized na study. The primary outcome is Number of Participants With Version of Fetal Breech Position to Cephalic Position up to 4 Weeks After Treatment.

2. Clinical Question

The trial record describes a randomized, parallel-group comparison. It indicates that randomization was stratified separately for primigravida and multiparae. The primary outcome counts participants with version from breech to cephalic position; it is not a measure of the degree or timing of version. The record says fetal position was checked in week 36-37 and external cephalic version was offered to participants still in breech position. Thus, the clinical question concerns the recorded position outcome over the stated follow-up, in a study context that also included an offer of external version for persistent breech presentation.

The available results show 34 of 48 participants in the moxibustion primiparae group and 34 of 44 in the control primiparae group with the outcome. For multiparae, the record lists 25 of 54 in each group. These are group counts, not a basis for inferring an individual participant’s outcome or the cause of a position change. The registry’s sponsor-reported analyses compare the randomized groups within parity strata. Their estimates and uncertainty are the principal results to use because a discrepancy is flagged between the sponsor analyses and the posted unadjusted recalculations.

3. Trial Design

The registry describes a randomized, parallel-group trial with enrollment of 200. The study is marked completed. Its listed start and primary completion dates are 2003-01 and 2011-01. The sponsor is Herning Hospital. Phase is recorded as not applicable. These record fields describe the study’s administrative and design context; they do not establish the rationale for the enrollment target or explain the duration between the recorded dates.

Women were randomized in week 32 to moxibustion or no moxibustion. The moxibustion regimen was daily treatment at Bl 67 for 15-20 minutes from week 32 to 36. Control participants received no intervention, with routine control schedules described separately for primiparae and multiparae. The registry says randomization was stratified by primigravida and multiparae separately. It describes an even-or-odd random-number procedure and a sealed, non-transparent envelope held on the obstetrical department, drawn when informed consent was given. Allocation concealment details beyond that description are not reported in the registry record.

Masking is listed as none. The registry therefore does not describe blinded participants or study personnel. At week 36-37 fetal position was checked, and external cephalic version was offered to those still in breech position. The primary outcome is the number of participants with a change from breech to cephalic position up to 4 weeks after treatment. The record lists one outcome measure and two sponsor-reported analyses, comparing moxibustion with control separately for primiparae and multiparae. Further details of the analysis population, missing outcome handling, and original statistical plan 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 Number of Participants With Version of Fetal Breech Position to Cephalic Position up to 4 Weeks After Treatment, measured over 4 weeks.

The primary endpoint counts participants whose fetal position changed from breech to cephalic within 4 weeks after treatment. The measure is reported as a number of participants with the event, alongside the number in each group. In the registry counts, 34 of 48 moxibustion primiparae and 34 of 44 control primiparae had the recorded outcome. Among multiparae, the listed counts are 25 of 54 in each group.

This is a binary endpoint: for each participant, the outcome is counted as having occurred or not having occurred within the stated period. Such endpoints can be clinically interpretable because they report how many participants experienced a defined event, rather than a change in a continuous measurement. General explanation: a binary endpoint does not describe when within follow-up the event occurred, how long a change lasted, or any intermediate changes in position. Those details are not reported in the registry record.

The endpoint fits the trial’s stated aim of evaluating version from breech to cephalic position. The record says fetal position was checked in week 36-37 and that external cephalic version was offered to participants still in breech position. It does not report further detail on outcome ascertainment, adjudication, or how the endpoint was handled for participants with missing position information. Those omissions limit what can be concluded about the exact measurement process, but do not change the endpoint definition recorded for the trial.

7. Results Posted in the Registry

• Moxibustion in Primiparae: 70.8% (34/48) versus 77.3% (34/44) on control; risk difference -6.4 percentage points (95% CI -24.3 to 11.4), risk ratio 0.92 (0.72–1.17); unadjusted two-proportion z-test p = 0.482.
• Moxibustion in Multiparae: 46.3% (25/54) versus 77.3% (34/44) on control; risk difference -31.0 percentage points (95% CI -49.1 to -12.8), risk ratio 0.60 (0.43–0.83); unadjusted two-proportion z-test p = 0.002.
• Control Multiparae: 46.3% (25/54) versus 77.3% (34/44) on control; risk difference -31.0 percentage points (95% CI -49.1 to -12.8), risk ratio 0.60 (0.43–0.83); unadjusted two-proportion z-test p = 0.002.

8. Statistical Interpretation

9. Statistical Methods Explained

The record identifies a randomized, parallel-group design. Random assignment is intended, in general, to create comparison groups that differ through assignment to the intervention rather than systematic selection. This trial also states that randomization was stratified by primigravida and multiparae separately. Stratification means assignment was organized within those participant categories, which supports the registry’s separate reporting for primiparae and multiparae. The record does not give enough detail to evaluate implementation beyond its description of a random-number procedure and sealed, non-transparent envelopes.

What does a risk ratio express?

A risk ratio compares the proportion with an outcome in one group with the proportion in another. A value of 1 represents equal proportions on this relative scale; values above or below 1 represent a higher or lower proportion in the numerator group, depending on the comparison’s specified direction. General explanation: a risk ratio is relative, so it does not by itself convey the absolute size of any difference. The registry’s sponsor analyses report risk ratios for the primiparae and multiparae comparisons. Their estimates are 1.17 and 1.0, respectively.

What does a risk difference express?

A risk difference subtracts one group’s event proportion from the other group’s proportion. It is an absolute-scale measure, commonly described in percentage-point terms when converted to that scale. The recalculated risk difference for primiparae is -0.064, with a confidence interval from -0.243 to 0.114. Its sign reflects the order used for the calculation, so the comparison order must be known before interpreting direction. The multiparae recalculation has a comparator-input problem: it uses 34 of 44, the control primiparae counts, rather than the listed control multiparae counts. It therefore should not be read as an unadjusted multiparae comparison.

Why are confidence intervals important?

A confidence interval describes the uncertainty around an estimate under the statistical method used. General explanation: a wider interval indicates less precision, while a narrower interval indicates greater precision. For the sponsor-reported risk ratios, the primiparae interval is 0.77 to 1.76 and the multiparae interval is 0.69 to 1.46; both include 1. These intervals leave room for effects on either side of no relative difference. A confidence interval is not a guarantee that the true effect lies within its limits, and it does not account for limitations that the analysis did not address.

What does the p-value add?

The sponsor reports p = 0.48 for primiparae and p = 1.00 for multiparae. General explanation: a p-value measures how unusual data at least as far from the null model as those observed would be if that model and the analysis assumptions held. It is not the probability that the null is true, nor a measure of clinical importance. The p-values should be considered alongside the effect estimates and confidence intervals, rather than as stand-alone decisions.

Why does the discrepancy matter?

The posted calculations are labeled as unadjusted recalculations from summary statistics, and the registry flags a discrepancy. In the primiparae comparison, the recalculated risk difference is not the same measure as the sponsor’s risk ratio, and the recalculated risk ratio also differs from the sponsor’s reported estimate. In the multiparae calculation, the control inputs match the primiparae control group, not the multiparae control group. A third calculation duplicates that same multiparae result. These issues prevent the recalculations from serving as a dependable substitute for the sponsor analyses. The sponsor’s own analysis takes precedence.

General explanation: an unadjusted calculation uses the group summaries directly and does not account for other covariates or design features beyond those represented in its inputs. It can be useful as a check, but it may not reproduce the sponsor’s method, analysis population, or handling of the data. The registry does not report the sponsor’s full statistical methods, so the reason for the differences is not established.

What can the record establish about analysis choices?

The registry lists two reported analyses and one primary outcome measure, but does not report a full statistical analysis plan. The original rationale for the enrollment target, prespecified handling of multiplicity, missing-data procedures, and analysis population are not reported in the registry record. It would therefore be inappropriate to infer those choices from the posted results. General explanation: without these details, readers cannot fully assess whether all planned comparisons are represented, how incomplete outcome information was treated, or whether the analysis followed a prespecified plan.

10. Confidence Intervals and Precision

The sponsor-reported estimates have substantial uncertainty. For primiparae, the risk ratio is 1.17 with a 95% confidence interval from 0.77 to 1.76. For multiparae, the risk ratio is 1.0 with a 95% confidence interval from 0.69 to 1.46. Each interval includes 1, the value corresponding to no relative difference. The intervals also extend to values on both sides of 1, so the data do not identify a narrow range of relative effects.

General explanation: a confidence interval summarizes sampling uncertainty under the analysis method. Its width is informative about precision, but it does not resolve possible measurement, selection, or analysis problems. Nor does it automatically account for multiple comparisons or missing outcomes. The registry does not report enough information to assess those issues fully.

The unadjusted primiparae risk-difference recalculation is -0.064, with a confidence interval from -0.243 to 0.114. This interval spans zero, but the registry flags a discrepancy between recalculation and sponsor analysis. The multiparae recalculation uses the control primiparae counts, so it should not be used to characterize precision for the multiparae comparison. The sponsor’s own analyses take precedence over the recalculations.

Precision is distinct from whether an estimate reaches a conventional significance threshold. A confidence interval can include the null value while still allowing effects that could matter in either direction. The sponsor’s estimates and intervals should therefore be read as uncertain comparisons, not as proof of equivalence or proof of a particular effect size.

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 sample-size figures are planning illustrations based on fractions of the observed effect, not the trial’s original design assumptions. The registry’s original sample-size justification and planning assumptions are not reported in the registry record. The figures are participants per arm, not total event counts. The listed assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the planning target changes when the assumed effect is reduced. General explanation: smaller effects are harder to distinguish from random variation, so detecting them at the same chosen power generally requires more participants. The columns for 80% and 90% power give the number of participants per arm needed, under those planning assumptions, to have the stated chance of detecting the specified effect if it is present. A 90% target is more demanding than an 80% target and generally calls for a larger planned sample.

These figures are not observed power and do not show the probability that the completed trial’s result is correct. They are hypothetical design illustrations computed from observed estimates. Because the registry flags a discrepancy in the posted recalculations, the figures should be interpreted cautiously, especially where they rely on the problematic multiparae contrast. They are not evidence that the trial was designed around those targets or that the trial had the corresponding power.

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 = 0.773; treatment proportion p₁ = 0.708; average p̄ = 0.741.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6199 = 1.2150.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6182 = 0.5203.
4. n = (1.2150 + 0.5203)² / (-0.0644)² = 726.2, rounded up to 727 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 <- 0.772727272727273                          # control proportion
p1 <- 0.708333333333333                          # 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(2251886)
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 = 727 (80% power), 972 (90% power)
 75% of observed effect: n per arm = 1,266 (80% power), 1,694 (90% power)
 50% of observed effect: n per arm = 2,788 (80% power), 3,731 (90% power)
power.prop.test: 726.2 
Simulated power at n = 727 per arm: 0.798 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The registry reports two sponsor analyses using chi-squared methods and risk ratios. For primiparae, the sponsor reports a risk ratio of 1.17, a 95% confidence interval from 0.77 to 1.76, and p = 0.48. For multiparae, the reported risk ratio is 1.0, the 95% confidence interval is 0.69 to 1.46, and p = 1.00.

The posted unadjusted recalculations do not fully align with those results. The primiparae recalculated risk difference is -0.064, while the sponsor reports a risk ratio; the recalculated risk ratio also differs from the sponsor’s reported estimate. For multiparae, the recalculation lists control inputs of 34 of 44, which belong to the control primiparae group, rather than the multiparae control count of 25 of 54. A second listed multiparae calculation duplicates that result. The registry marks a discrepancy.

Accordingly, the sponsor’s own analyses take precedence over the recalculations. The record does not explain why the estimates differ, and it does not report enough detail to resolve the discrepancy independently. The recalculated values should not be substituted for the sponsor’s reported subgroup comparisons.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and two reported analyses, with sponsor comparisons for primiparae and multiparae. It does not report a multiplicity adjustment, a hierarchy among the subgroup comparisons, or a prespecified plan for handling multiple tests. Therefore, whether multiplicity was considered in the original analysis is not reported in the registry record.

General explanation: when several hypotheses are tested, the chance of at least one apparently unusual result can increase if each test is interpreted independently. Whether adjustment is appropriate depends on the analysis plan and the role of each comparison. The posted record does not establish that an adjustment was required or omitted; it simply does not describe the plan. The subgroup-specific sponsor results should be understood in that context rather than assumed to represent a single overall treatment effect.

The record gives group outcome counts but does not report missing outcome counts, reasons for missingness, or a method for handling missing data. It also does not state whether the reported analyses followed an intention-to-treat, per-protocol, or other analysis population. The stated enrollment is 200, but enrollment alone does not identify which participants were included in each outcome analysis or how absent measurements were treated.

General explanation: missing outcomes can affect interpretation if the probability of missingness differs between groups or is related to the outcome. Without a description of completeness and handling, readers cannot assess that possibility from the registry entry. The record also does not report a full statistical analysis plan or whether additional planned analyses were conducted. These absences are reporting limitations; they do not by themselves show that the analyses were biased or that data were missing.

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 0% reporting threshold.

The adverse-event entries list zero serious adverse events and zero other adverse events for each of the four groups. The registry lists no serious adverse-event terms. Death counts are recorded as null, which means deaths are not reported in the registry record; null should not be read as a count of zero.

These entries describe what the registry reports for the specified groups. They do not establish that every possible adverse effect was actively assessed or that no unlisted event occurred. The record does not provide further detail on adverse-event definitions, collection procedures, follow-up for safety, or completeness of reporting. General explanation: a zero count in a registry field means no events were entered for that field, and interpretation depends on how events were sought and recorded. The entries should therefore be read as limited safety reporting rather than as proof of absence of harm.

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

The sponsor-reported results do not show a clear relative difference between moxibustion and control in either parity subgroup. For primiparae, the risk ratio is 1.17 with a 95% confidence interval from 0.77 to 1.76 and p = 0.48. For multiparae, the risk ratio is 1.0 with a 95% confidence interval from 0.69 to 1.46 and p = 1.00. Both confidence intervals include 1 and span values on either side of it, leaving uncertainty about the size and direction of any relative difference.

The posted event counts are 34 of 48 versus 34 of 44 for primiparae, and 25 of 54 versus 25 of 54 for multiparae, comparing moxibustion with control. The registry also flags a discrepancy between sponsor analyses and unadjusted recalculations. The multiparae recalculation uses control counts from the primiparae group, so it should not be used as a valid subgroup estimate. The sponsor’s own analyses take precedence.

These results do not establish that the groups are equivalent, nor do they establish a particular treatment effect. A nonsignificant p-value is not proof of no difference. General explanation: a result can be statistically uncertain because the estimate is imprecise, even when the observed counts are similar. The confidence intervals communicate that uncertainty, while the discrepancy and missing reporting details limit interpretation further.

The registry describes an open-label randomized trial and a primary outcome of fetal position change within 4 weeks after treatment. It also reports that external cephalic version was offered to participants still in breech position at the week 36-37 check. The reported endpoint therefore belongs to that study context; the record does not isolate the contribution of each aspect of care to a position change. No medical advice follows from these registry results alone.

17. Why This Trial Matters Statistically

This record illustrates why results should be read at the level of the comparison actually reported. The trial separates primiparae and multiparae, and the sponsor reports a risk ratio for each group. Those estimates have confidence intervals that include 1 and extend on either side, so the point estimates alone do not convey the uncertainty.

It also demonstrates why a recalculation is a check rather than an automatic replacement for the sponsor’s analysis. The registry flags a discrepancy, and the multiparae recalculation uses the control primiparae counts. Recognizing that mismatch prevents a cross-stratum calculation from being mistaken for the intended subgroup comparison. In this case, the sponsor’s own analyses take precedence.

General explanation: randomized assignment can support a comparison of groups, but sound interpretation still depends on accurate group definitions, outcome ascertainment, analysis choices, and transparent reporting. A binary endpoint is straightforward to count, yet its interpretation depends on what was measured, when it was assessed, and how missing information was handled. The registry provides some of that context but not all of it.

The sample-size illustrations also show the difference between planning and inference. They use the observed effect as a planning reference and specify assumptions that are not reported as the trial’s original design plan. Such illustrations can help readers understand how assumed effect size affects planning, but they do not demonstrate that the completed trial was designed for those targets or that it had a particular 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 does not report the original sample-size rationale or the trial’s original design assumptions. It does not provide a full statistical analysis plan, an analysis-population definition, or details of missing-data handling. These omissions make it difficult to assess whether the posted analyses followed prespecified methods or how incomplete outcome information may have affected results.

The study is listed as unmasked. The registry does not report additional safeguards for outcome assessment or whether the position outcome was assessed by personnel unaware of allocation. It also does not describe the exact outcome ascertainment procedure beyond checking fetal position in week 36-37 and defining the endpoint over 4 weeks after treatment. Further information on adherence to daily moxibustion, protocol deviations, and the timing of outcome measurement is not reported in the registry record.

A discrepancy is flagged between the sponsor analyses and posted recalculations. In particular, the multiparae recalculation uses counts listed for control primiparae, and another listed calculation duplicates that result. This makes the recalculated multiparae contrast unsuitable for interpretation as a within-parity comparison. The sponsor’s own analysis takes precedence, but the reason for the discrepancy is not reported.

The registry reports no secondary outcomes and gives limited safety detail. Serious and other adverse-event counts are listed as zero in each group, while deaths are not reported. The record does not describe how adverse events were collected or establish the completeness of those entries. These are limits on what can be concluded from the registry record, not evidence that unreported events occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Moxibustion in a Randomized Trial for Version of Breech Position From Week 32 — NCT02251886.
• Registry record last updated 2017-03-03; status last verified 2017-01.
• Results first posted 2016-12-01.
• 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

This completed randomized, parallel-group trial record concerns moxibustion for singleton breech position before term. Participants were assigned in week 32 to daily moxibustion at Bl 67 or no moxibustion, with results reported separately for primiparae and multiparae. The primary outcome counts version from breech to cephalic position up to 4 weeks after treatment.

The sponsor reports risk ratios of 1.17 for primiparae and 1.0 for multiparae; both confidence intervals include 1. The registry flags discrepancies with posted unadjusted recalculations, including a multiparae calculation using primiparae control counts. The sponsor’s own analyses take precedence. Details of the original sample-size justification, analysis population, missing-data handling, multiplicity plan, and full statistical methods are not reported in the registry record.