CO2 Versus Lund De-airing Technique in Heart Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for CO2 Versus Lund De-airing Technique in Heart Surgery (NCT00934596), a randomized na study. The primary outcome is Number of Air Microemboli Registered Over the Middle Cerebral Arteries by On-line Trans-cranial Echo-Doppler (TCD)..

2. Clinical Question

The primary measure combined gaseous microembolic signals counted from the right and left cerebral arteries. The results are therefore about the total signals recorded across those arteries during the specified interval, rather than a separate result for each side. The registry also describes counting signals after cardiac ejection and during the period after cardiopulmonary bypass, but the posted primary outcome is the before-ejection measure.

The result is a comparison of observed groups in a randomized trial, not a direct estimate of every aspect of de-airing performance. The registry lists additional outcomes related to de-airing time and cardiopulmonary bypass, but those outcomes do not replace the primary endpoint. The aims also included cost effectiveness and side effects; cost-effectiveness results are not reported in the registry record.

The primary statistical contrast is reported in two ways: the sponsor's analysis uses a Wilcoxon (Mann-Whitney) method and reports a net median difference, while a recalculation from the posted means and standard deviations estimates a difference in means. Those measures answer related but distinct statistical questions. Because the registry flags a discrepancy between the sponsor's analysis and the recalculation, the sponsor's own analysis takes precedence when describing the trial's reported result.

3. Trial Design

The registry describes a randomized, parallel-group trial, with no masking. The study is listed as completed and was sponsored by Lund University. The condition recorded is aortic valve disorder. The registry lists the phase as NA. Enrollment is recorded as 20, with 10 participants in each posted arm.

The trial began in 2009-06, and primary completion is recorded as 2009-10. One arm received the Lund de-airing technique; the other received carbon-dioxide insufflation delivered to the open mediastinal wound in a standardized manner. The record identifies the comparison as taking place in open left heart surgery, where the left heart is exposed to ambient air. It does not report the details of the randomization sequence, allocation concealment, or the rationale for the planned enrollment.

Because masking is listed as none, the trial was open-label in the sense that masking was not used. The registry does not explain whether outcome assessors were masked separately, so that detail is not reported in the registry record. The record also does not report a formal sample-size justification or the original design assumptions. The planning figures calculated from the observed effect should not be mistaken for the trial's original enrollment plan.

The registry lists 12 outcome measures and 3 analyses, including the primary measure and secondary measures such as total de-airing time, de-airing time before and after cardiac ejection, oxygenator gas flow at 45 minutes of cardiopulmonary bypass, and pH at 45 minutes of cardiopulmonary bypass. Five secondary outcomes are posted in the record. The listed aims additionally include cost effectiveness and possible side effects, but cost-effectiveness results are not reported in the registry record.

The parallel-group design compares outcomes between participants assigned to different techniques. Randomization can help balance factors between groups on average, but it does not ensure that every characteristic is balanced in a small trial. The registry does not report baseline characteristics, so the extent of balance on measured participant characteristics cannot be assessed from this record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: All 20 consecutive patients recruited in the study fullfilled the inclusion criteria. No patient was excluded.

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 Air Microemboli Registered Over the Middle Cerebral Arteries by On-line Trans-cranial Echo-Doppler (TCD)., measured over Before cardiac ejection.

The primary endpoint is the number of air microemboli registered over the cerebral arteries before cardiac ejection. The registry describes these signals as gaseous microembolic signals. They were counted concurrently in the right and left cerebral arteries, and the signals from both sides were summed to create the recorded total. The endpoint is a continuous count measure, summarized in the posted results as a mean and standard deviation for each arm.

This measure is relevant to the stated study question because the investigators aimed to compare de-airing methods in relation to cerebral air emboli during open left heart surgery. A signal count provides a measure of detected microembolic activity in the specified monitoring interval. It is not, by itself, a direct measure of a patient's symptoms, later neurological function, or clinical outcome. Those outcomes are not described as the primary endpoint in the registry record.

The registry's primary time frame is before cardiac ejection. Its outcome description also refers to counting during intervals after cardiac ejection and after cardiopulmonary bypass, but the posted primary summary concerns the before-ejection interval. The distinction matters: results from different intervals represent different periods of monitoring and should not be treated as interchangeable.

As a general statistical point, a count endpoint can vary substantially between participants. A mean describes the group average, while the standard deviation describes variation around that average. Neither alone gives the full distribution of counts or indicates how many participants experienced a clinical consequence. The registry record does not report participant-level counts or a clinical interpretation threshold for this measure.

7. Results Posted in the Registry

• Carbon-dioxide Insufflation Technique: mean 118.00 versus 41.00 on control; difference 77.00 (95% CI 31.88 to 122.12), standardized effect d = 1.50; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the mean difference describe?

A mean is the arithmetic average of the observed values in an arm. The recalculated mean difference compares the carbon-dioxide arm's mean with the Lund arm's mean. The reported estimate is 77.0 air microemboli, with a confidence interval of 31.88 to 122.1. This is an unadjusted recalculation from the posted summary statistics; it is not the sponsor's reported test result.

As a general statistical explanation, a difference in means is useful when the research question is about average outcome levels. It can be sensitive to unusually high or low observations, especially when observations vary widely. The posted summaries show a larger standard deviation in the carbon-dioxide arm, but without participant-level data the distributions and influence of individual values cannot be assessed.

How does the sponsor's rank-based analysis differ?

The sponsor reports a Wilcoxon (Mann-Whitney) analysis and a net median difference of 57, with p <0.01. In general, this test uses the ordering of observations rather than comparing group means directly. Its result is not automatically a test of the difference between medians in every setting; interpretation depends on assumptions about the distributions. The record does not describe those assumptions or provide the individual observations needed to examine them.

The two analyses therefore do not have to produce the same numerical estimate or p-value. One is a recalculated difference in means based on arm summaries; the other is the sponsor's reported rank-based analysis. The registry explicitly flags a discrepancy. Accordingly, the sponsor's own analysis takes precedence as the reported trial analysis, while the recalculation can be read as a separate, unadjusted summary-statistic comparison.

What does the p-value tell the reader?

In general, a p-value measures how compatible data are with a specified null hypothesis under the assumptions of a statistical model. It is not the probability that an observed difference arose by chance, and it does not measure clinical importance. The reported unadjusted recalculation has p <0.001; the sponsor's Wilcoxon analysis has p <0.01. They refer to different analyses and should remain distinct.

The registry does not report whether the analysis plan specified a primary statistical test in advance, whether there were interim analyses, or whether any adjustment was made for multiple outcomes or comparisons. These details are not reported in the registry record. Without them, the p-values should be read as the results of the analyses identified in the record, not as evidence that all analytic choices or repeated testing have been accounted for.

Why do standard deviations matter?

A standard deviation describes dispersion around a mean. The posted standard deviations are 20.0 for Lund de-airing and 70.0 for carbon-dioxide insufflation. General statistical reasoning: when outcome variability is large relative to the group size, estimates can be less stable and sensitive to the observations included. Count data may also have distributions that are asymmetric or contain many low values and some high values; that is a general feature to consider, not a distributional finding established for these participants. The registry does not post enough information to assess the distribution directly.

The recalculation includes a pooled standard deviation of 51.48 and a standardized difference of 1.496. A standardized difference expresses a contrast in relation to a variability scale, which can aid comparison across settings using different units. It does not replace the original-unit difference, explain clinical importance, or correct for the discrepancy with the sponsor analysis.

What can and cannot be inferred from randomization?

Random assignment is intended to reduce systematic differences between treatment groups at allocation. It does not guarantee that all prognostic characteristics will be balanced, particularly in a small trial. The registry identifies the study as randomized but does not report the sequence-generation or concealment methods, baseline characteristics, or an analysis population. Those details are not reported in the registry record.

The record does not report whether the primary analysis followed an intention-to-treat principle, how protocol deviations were handled, or how missing outcome values were treated. Those omissions limit assessment of whether the reported groups and endpoint summaries reflect all randomized participants. The presented arm summaries list 10 participants per arm, but that alone does not establish how missing observations or exclusions were handled for each analysis.

In general, the strength of an analysis depends not only on the test name but also on the outcome definition, data completeness, assumptions, and analysis population. The registry's posted information supports describing the reported arm summaries and identified analyses. It does not support reconstructing the full statistical plan or determining whether unreported analytic decisions altered the result.

10. Confidence Intervals and Precision

The recalculated mean difference is 77.0 air microemboli, with a confidence interval from 31.88 to 122.1. The interval describes uncertainty around the estimated difference under the recalculation's assumptions. Its range includes values appreciably below and above the point estimate, so the point estimate should not be read as an exact value for the underlying contrast.

As a general explanation, a confidence interval is a method for expressing the precision of an estimate. A wider interval indicates less precision than a narrower interval, all else equal. It is not a range containing a stated proportion of individual participants' outcomes, and it does not mean that there is a particular probability that the fixed underlying effect lies within this particular calculated interval. The registry provides no confidence-interval bounds for the sponsor's Wilcoxon analysis.

The arm summaries also show standard deviations of 20.0 and 70.0. These describe variation in the observed counts within each arm; they are not confidence intervals for the means. The larger standard deviation in the carbon-dioxide arm signals greater observed dispersion, but the individual data are not reported. The posted summaries therefore cannot show whether the variation reflects a broadly spread distribution or a small number of particularly high counts.

The trial's enrollment was 20, with 10 participants in each arm. In general, estimates from small groups can be imprecise, and single observations can have a substantial influence on summaries. The reported interval quantifies uncertainty for the recalculated mean contrast, but it does not address all uncertainty, including potential missing data, analysis choices, or the discrepancy with the sponsor's result. Because the sponsor's reported analysis differs in method and estimand, the recalculated interval should not be used as if it were a confidence interval for the sponsor's net median difference.

The sponsor analysis is reported with a 95% confidence level, but its interval bounds are not reported in the registry record. Without those bounds, its precision cannot be assessed from the posted analysis fields. The inferential results should therefore be read with both the method difference and the limited precision of the small study in mind.

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. The registry's planning assumptions specify a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The detectable effect is set as a stated fraction of the observed effect. The trial's original design assumptions and sample-size justification are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 8 participants per arm for 80% power and 10 participants per arm for 90% power. Planning for 75% of the observed effect gives 13 participants per arm for 80% power and 17 participants per arm for 90% power. Planning for 50% of the observed effect gives 29 participants per arm for 80% power and 38 participants per arm for 90% power.

In plain language, the 80% power column gives the illustrated arm size associated with an 80% chance of detecting the specified effect under the stated planning assumptions, if that effect and assumptions were true. The 90% power column applies the same idea at a higher target chance of detection. These are planning illustrations based on the observed effect, not observed power.

The pattern across the rows illustrates a general principle: smaller effects require more participants to detect them at a chosen power level, all else being equal. The calculations are not evidence that the trial was originally designed with those group sizes or assumptions. They also do not establish that a future study would achieve the stated power if its actual effect, variability, allocation, or analytic method differed from the planning setup.

The sample-size illustration is based on the recalculated observed effect, while the sponsor's reported analysis uses a rank-based method and a net median difference. The registry does not report planning assumptions tied to that sponsor analysis. The figures should therefore be treated as conditional planning guidance for the stated mean-based effect illustration, not as a direct design recommendation for the sponsor's analysis or a guarantee of a future study's result.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 77.000; pooled standard deviation σ = 51.478.
2. n = 2 × (1.96 + 0.842)² × 51.478² / 77.000² = 7.0, rounded up to 8 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
delta <- 77                      # observed difference in means
sigma <- 51.478150704935                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(934596)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 8 (80% power), 10 (90% power)
 75% of observed effect: n per arm = 13 (80% power), 17 (90% power)
 50% of observed effect: n per arm = 29 (80% power), 38 (90% power)
power.t.test: 8.1 
Simulated power at n = 8 per arm: 0.797 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 own reported analysis used the Wilcoxon (Mann-Whitney) method and gives a net median difference of 57, with p <0.01. The registry does not report confidence-interval bounds for this estimate. That analysis is distinct from the recalculation based on posted means and standard deviations, which estimates a mean difference of 77.0, with a confidence interval of 31.88 to 122.1 and an unadjusted p-value of <0.001.

The estimates are not interchangeable: the sponsor reports a rank-based comparison and a net median difference, while the recalculation compares means. The record flags a discrepancy between them. The sponsor's own analysis takes precedence as the trial's reported analysis; the recalculated comparison is useful as a separate description of the posted summary statistics, not a replacement for the sponsor's result.

The registry does not explain the discrepancy or provide enough participant-level data to reproduce the sponsor's analysis independently. Differences in estimand and method are clear, but the record does not establish that they fully explain the differing results. The sponsor's reported p-value should not be interpreted as confirming the recalculated mean difference, nor should the recalculated confidence interval be attributed to the sponsor analysis.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 12 outcome measures and 3 analyses, and it posts 5 secondary outcomes. The primary outcome description includes monitoring at more than one interval, while the posted primary endpoint is the before-ejection measure. Multiple outcomes and analyses can create opportunities for chance findings when many statistical tests are conducted. As a general statistical principle, a multiplicity strategy can address that issue, but the registry does not report whether an adjustment was planned or used. The status of any multiplicity control is not reported in the registry record.

The record does not report whether the primary endpoint and analysis were prespecified in a statistical analysis plan, whether outcomes were selected after results were examined, or whether interim analyses occurred. These details are not reported in the registry record. The p-values should therefore be understood as the values reported for the identified analyses, without assuming that they account for testing across the full set of outcomes.

Missing-data handling is also not reported in the registry record. The posted arm summaries list 10 participants per arm, but the record does not explain whether all randomized participants contributed to the primary endpoint, whether any values were missing, or how missing observations were handled. It does not report reasons for missingness, imputation methods, or sensitivity analyses.

The analysis population is not reported in the registry record. In particular, the record does not state whether the sponsor analysis included all randomized participants, only participants with observed measurements, or another defined population. Randomization is listed, but the result cannot be fully evaluated without knowing how assignment, exclusions, and outcome availability were handled in the analysis.

The registry also does not report the detailed statistical analysis plan, including any adjustment for baseline characteristics or prespecified handling of protocol deviations. These omissions do not invalidate the posted results, but they limit independent assessment of analytic choices and the relationship between the reported findings and the original plan.

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 registry reports zero serious adverse events among 10 participants at risk in the Lund de-airing group and zero among 10 participants at risk in the carbon-dioxide insufflation group. No serious adverse-event terms are listed. These are the serious-event figures recorded for the groups; they do not establish that serious harms are impossible or that the techniques have equivalent safety.

For other adverse events, the registry records 1 among 10 participants at risk in each group. Death counts are not reported in the registry record. The safety information should be interpreted as a limited set of recorded counts rather than a complete account of every possible event or a definitive comparison of risks.

As a general statistical point, a trial with small groups has limited ability to detect uncommon adverse events, and a zero count does not mean the underlying risk is zero. The record does not provide event descriptions for the serious-event category, detailed severity or timing information, or a comparative statistical analysis of adverse events. The study's stated aim included assessing possible side effects, but these counts alone cannot resolve broader safety questions.

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

The posted primary summaries show mean air-microemboli counts of 41.0 for Lund de-airing and 118.0 for carbon-dioxide insufflation before cardiac ejection. The recalculated mean difference is 77.0, with a confidence interval of 31.88 to 122.1 and unadjusted p <0.001. Separately, the sponsor's Wilcoxon (Mann-Whitney) analysis reports a net median difference of 57 and p <0.01. Because the registry flags a discrepancy, the sponsor's own analysis takes precedence as the reported trial analysis.

The result does not establish that either technique changes patient-important outcomes. The endpoint is a monitored count of gaseous microembolic signals, not a reported neurological outcome or measure of later function. Nor does the result establish an overall clinical benefit or harm. The registry's primary result does not answer the separate questions about total de-airing time, cost effectiveness, or all possible side effects.

The trial had 10 participants in each arm, and no masking was used. The registry does not report baseline characteristics, detailed randomization procedures, missing-data handling, or the analysis population. Those gaps limit assessment of comparability, potential bias, and the completeness of the analysis. The greater variability in the carbon-dioxide arm also cautions against treating its mean as a full description of the distribution of observed counts.

Statistical significance is not a measure of clinical importance. The estimates describe a difference in the recorded endpoint under the respective analyses; they do not establish whether the magnitude matters to patients or clinicians. The registry does not provide a clinical threshold for interpreting the signal count. The result should therefore be viewed as a small-trial comparison of a specific monitoring outcome, not as a comprehensive verdict on the two de-airing approaches.

Finally, no cost-effectiveness result is reported in the registry record. The study's stated aims include costs and possible side effects, but the posted findings summarized in the primary outcome cannot be extended to those outcomes without their data.

17. Why This Trial Matters Statistically

This trial highlights how the choice of summary measure and test affects interpretation. A mean difference answers a question about average counts, while the sponsor's Wilcoxon (Mann-Whitney) analysis uses ranks and reports a net median difference. Those approaches can yield different estimates and p-values because they do not necessarily target the same statistical contrast. The registry flags a discrepancy, so retaining the distinction is essential; the sponsor's own analysis takes precedence as the reported result.

The arm summaries also show why variability deserves attention. The standard deviation is larger in the carbon-dioxide arm than in the Lund arm. General statistical reasoning suggests that a mean can be an incomplete description when observations are highly variable or asymmetric, and that small groups may not characterize a distribution reliably. The registry does not provide participant-level values, so the shape of the distributions and the influence of individual observations cannot be assessed.

The study's primary measure is a count of monitored signals during a defined surgical interval. That makes the outcome specific and measurable, but it is not the same as a patient-centered clinical endpoint. Statistical evidence about a signal count should not be silently translated into claims about symptoms, neurological outcomes, or overall safety.

The record also illustrates the value of complete reporting. Information about missing data, the analysis population, multiplicity, and original sample-size assumptions is not reported in the registry record. Without those details, readers can describe the posted estimates but cannot fully assess how the analysis relates to the original plan. For biostatisticians and clinical researchers, keeping the estimand, test, precision, and reporting gaps explicit is central to a fair interpretation.

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 enrollment was 20, with 10 participants in each arm. Such a small study provides limited information about outcome variability and can be sensitive to individual observations. The posted standard deviation is larger in the carbon-dioxide arm, while participant-level data are not reported, so the distribution of the primary outcome cannot be examined.

The trial was unmasked. The registry does not report whether outcome assessors were masked independently, so that detail is not reported in the registry record. It also does not describe the randomization sequence or allocation concealment. These omissions limit evaluation of possible bias and the conduct of group assignment.

The sponsor's reported rank-based result and the recalculated mean-based result differ in both method and estimand. The registry flags a discrepancy but does not explain it, and the individual observations needed to reproduce the analyses are not reported in the registry record. The sponsor's own analysis takes precedence; the summary-statistic recalculation should be considered separately.

Missing-data handling, analysis population, baseline characteristics, multiplicity adjustment, interim analyses, and the original sample-size justification are not reported in the registry record. The record lists multiple outcomes and analyses, but does not establish whether adjustments for repeated testing were used. The posted primary result therefore cannot be fully assessed against a detailed prespecified statistical plan.

The primary endpoint is a monitored microemboli count before cardiac ejection, not a direct measure of clinical neurological outcome. The registry lists additional de-airing and cardiopulmonary bypass outcomes, but the registry entries do not provide their results. Although the aims include cost effectiveness and possible side effects, cost-effectiveness results are not reported in the registry record. The serious adverse-event counts are limited and do not settle broader safety questions.

The registry identifies the condition and surgical setting but does not report detailed eligibility criteria or participant characteristics. The extent to which these findings apply to other patients or surgical settings cannot be assessed from the registry record alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: CO2 Versus Lund De-airing Technique in Heart Surgery — NCT00934596.
• Registry record last updated 2013-12-04; status last verified 2013-10.
• Results first posted 2013-12-04.
• 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

NCT00934596 is a completed, randomized, parallel-group trial sponsored by Lund University. It compared the Lund de-airing technique with carbon-dioxide insufflation in open left heart surgery and enrolled 20 participants, with 10 in each arm. The study began in 2009-06, and primary completion is recorded as 2009-10. Masking is listed as none.

The primary outcome was the number of air microemboli counted over the cerebral arteries before cardiac ejection. The sponsor reports a Wilcoxon (Mann-Whitney) analysis with a net median difference of 57 and p <0.01. A separate recalculation from the posted mean and standard deviation summaries estimates a mean difference of 77.0, with a confidence interval of 31.88 to 122.1 and unadjusted p <0.001. The registry flags a discrepancy, so the sponsor's own analysis takes precedence.

Serious adverse events were recorded for zero participants in each arm; other adverse events were recorded for 1 participant in each arm. Details about missing data, analysis populations, multiplicity, and original design assumptions are not reported in the registry record.