DAR-901 TB Booster Vaccine to Prevent TB in Adolescents: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for DAR-901 TB Booster Vaccine to Prevent TB in Adolescents (NCT02712424), a randomized phase 2 study. The primary outcome is New Infection With Mycobacterium Tuberculosis.

2. Clinical Question

The trial addresses prevention of infection, not treatment of tuberculosis disease. Its primary outcome was based on a change in IGRA status: conversion from negative to positive. The registry record also lists persistent new infection as a secondary outcome. These outcomes represent different definitions of infection in the trial record, so the secondary result should not be treated as a duplicate measure of the primary outcome.

The registry record describes the study as randomized and placebo-controlled. Its official title describes it as double-blind, while the structured masking entry is quadruple. The record does not explain which roles were included in that masking designation. The planned comparison is between participants assigned to the active vaccine and participants assigned to placebo; it does not establish that assignment or masking eliminated every possible source of bias.

3. Trial Design

This was a phase 2, randomized, placebo-controlled study with a parallel-group design. The registry record lists an enrollment of 625 participants and shows 315 participants in the DAR-901 group and 310 in the placebo group for the primary outcome. Participants were adolescents in Tanzania who had previously received BCG, according to the trial description. The study status is completed.

The intervention descriptions specify intradermal injections: 0.1 mL of DAR-901 containing 1 mg of the vaccine, or 0.1 mL of sterile saline for human use. The official title describes the study as double-blind; the structured masking entry is quadruple. The record does not identify the people included in that masking category or describe procedures used to maintain masking.

The primary outcome was new infection with Mycobacterium tuberculosis, measured as conversion from a negative to a positive IGRA result. The stated timeframe was 3 years. The registry record also lists persistent new infection with M. tuberculosis as a secondary outcome over 3 years. It gives counts of participants with each outcome, rather than a time-to-event estimate.

The record lists a start date of 2016-03 and a primary completion date of 2020-02-01. The original protocol’s detailed design assumptions, including the original sample-size justification, are not reported in the registry record. Nor does the record describe interim analyses or the exact analysis population used for each result. These omissions limit the ability to reconstruct how the final analysis followed the original plan.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Conversion from IGRA neg to pos

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 New Infection With Mycobacterium Tuberculosis, measured over 3 years.

The primary endpoint is the count of participants with new Mycobacterium tuberculosis infection, defined in the registry record as conversion from a negative to a positive IGRA result. The stated timeframe is 3 years. For this binary outcome, each participant is classified according to whether the event was recorded; the reported endpoint is the number of participants with an event in each group.

IGRA conversion is used as an indicator of newly detected infection. It provides an operational way to distinguish participants whose test status changed during follow-up from those without a recorded conversion. The record does not provide further detail about the testing schedule, confirmation rules, or how missing or indeterminate tests were handled, so those procedures cannot be inferred from the endpoint description alone.

The endpoint concerns infection rather than diagnosed tuberculosis disease. That distinction matters when interpreting the result: the primary comparison addresses recorded IGRA conversion, not every possible clinical outcome related to tuberculosis. The registry record also reports persistent new infection as a separate secondary outcome. Its count should be read according to that separate endpoint definition, rather than combined with the primary count.

In general, a binary endpoint is useful when the central question is whether an event occurred within a stated period. Its simplicity makes the group counts and absolute difference straightforward to interpret, but it does not convey the timing of events within follow-up. The registry record reports no time-to-event analysis for this outcome.

7. Results Posted in the Registry

• DAR-901: 6.0% (19/315) versus 5.8% (18/310) on control; risk difference 0.2 percentage points (95% CI -3.5 to 3.9), risk ratio 1.04 (0.56–1.94); unadjusted two-proportion z-test p = 0.905.

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.

Persistent New Infection With M. Tuberculosis

• 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:
  • DAR-901: 3.2% (10/315) versus 1.6% (5/310) on control; risk difference 1.6 percentage points (95% CI -0.8 to 4.0), risk ratio 1.97 (0.68–5.69); unadjusted two-proportion z-test p = 0.202.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DAR-901 and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists one secondary endpoint: persistent new infection with M. tuberculosis over 3 years. Its comparison has a different count pattern from the primary endpoint, but the uncertainty interval includes no difference. This secondary result does not overturn or resolve the primary finding. The two endpoints use related but distinct definitions, and they should be interpreted as separate outcome measures rather than combined into one result.

In general, secondary outcomes can help describe whether the pattern across a study’s measures is consistent or whether findings depend on the outcome definition. They can also generate questions for future research. They usually carry less confirmatory weight when the registry record does not describe a prespecified hierarchy, multiplicity adjustment, or detailed analysis plan. The record does not report such a plan for these outcomes.

When multiple outcomes are tested, the chance of obtaining at least one apparently notable result by chance can increase. In general, multiplicity procedures address that issue by adjusting how results are interpreted or tested. No such adjustment is reported in the registry record. The secondary comparison is unadjusted, and its p-value should not be treated as if it were the sole planned test in a study with no other outcomes.

The record lists no reported analyses for the secondary endpoint. That limits what can be assessed about the analytic procedure and whether the outcome was handled according to a prespecified approach. The overall pattern is best described cautiously: the secondary result differs numerically from the primary pattern, but the posted statistical uncertainty does not establish a clear group difference. It remains supportive context rather than a stand-alone conclusion.

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

• Persistent New Infection With M. Tuberculosis

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: the registry record counts participants with a recorded IGRA conversion. The comparison is therefore based on counts in the DAR-901 and placebo groups. In general, a binary outcome can be summarized as a risk in each group, an absolute difference between those risks, or a relative measure such as a risk ratio or odds ratio. Each summary emphasizes a different aspect of the contrast.

What does the risk difference describe?

The reported risk difference is 0.002. It expresses the absolute contrast between the group risks on the scale used by the analysis. The 95% confidence interval runs from -0.035 to 0.039. A value of zero on this scale corresponds to no absolute difference. Because the interval includes zero, the data are compatible with no difference as well as with differences in either direction. The interval’s endpoints also show why an estimate close to zero does not alone establish equivalence.

How do the relative measures differ?

The risk ratio compares the event risks as a ratio, and the odds ratio compares the event odds. The reported risk ratio is 1.039, with a 95% confidence interval from 0.556 to 1.941. The reported odds ratio is 1.041, with a 95% confidence interval from 0.536 to 2.024. In general, a ratio of one represents no relative difference. Both intervals include one, and both allow for effects in either direction. Risk ratios and odds ratios are not interchangeable in general, even when their estimates are close in a particular result.

What does the p-value add?

The unadjusted p-value for the primary comparison is 0.905. In general, a p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the test. It does not give the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The p-value should be interpreted with the effect estimates and confidence intervals. Here, the estimate is near zero, the interval includes no difference, and the unadjusted p-value does not indicate evidence against the null model.

Why is the analysis called unadjusted?

The comparison is reported as unadjusted. In general, an adjusted analysis accounts for specified variables or features of the study design, while an unadjusted comparison uses the group outcome information without such statistical adjustment. The registry record does not report an adjusted primary analysis, the covariates that might have been considered, or the statistical model used to produce the posted comparison. No additional model details should be assumed.

What does randomization contribute?

Random allocation is intended to make the assigned groups comparable on average at the start of a trial, including with respect to characteristics not explicitly measured. The registry record describes the allocation as randomized and the design as parallel. Randomization does not remove the need to examine follow-up, outcome ascertainment, adherence, and missing data. The record does not report those details in a way that permits a full assessment of their effects on the analysis.

What is the role of masking?

The official title describes the trial as double-blind, while the structured masking entry is quadruple. In general, masking can reduce the chance that knowledge of assignment influences care, participant reports, or outcome assessment. The record does not clarify who was masked or how masking was maintained. The labels therefore describe the registered design but do not, by themselves, demonstrate that masking was successful.

Why can rare events make estimates imprecise?

In general, when an outcome is uncommon, the group comparison may depend on a relatively small number of events. Estimates can then be sensitive to a small change in the event count, and confidence intervals may be broad. The primary results have 19 events in the DAR-901 group and 18 in the placebo group. The uncertainty intervals are more informative about the range of compatible differences than the small separation between the counts alone.

What can be inferred from the analysis record?

The registry record lists zero analyses and includes no reported sponsor analysis. It also does not report the original sample-size justification, interim analysis plan, missing-data methods, or analysis populations. In general, these details help readers assess whether a final analysis followed the intended plan and how sensitive the findings may be to analytic choices. Their absence means the posted results cannot be fully checked against a detailed prespecified statistical plan.

The statistical interpretation is therefore anchored to the posted counts and comparison estimates. The simple unadjusted comparisons describe the observed groups, while the record’s limited analysis detail leaves open questions about the exact inferential procedure and handling of incomplete outcome data. Those uncertainties do not erase the reported estimates, but they define the scope of what can be concluded from them.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.002, and its 95% confidence interval extends from -0.035 to 0.039. A confidence interval describes a range of values compatible with the observed data under the statistical method used. In repeated use of the same method under its assumptions, intervals constructed this way have the stated coverage. It is not a range containing a known effect with a probability attached to this particular trial.

Because the primary interval crosses zero, it does not isolate a direction of difference. Its lower endpoint is negative and its upper endpoint is positive. Thus, the results are compatible with a lower event risk in the DAR-901 group, little or no difference, or a higher event risk. The interval is not narrow enough to treat the point estimate as a precise estimate of the underlying group difference.

The relative-scale intervals also span the no-difference value of one: 0.556 to 1.941 for the risk ratio and 0.536 to 2.024 for the odds ratio. These intervals allow a broad range of relative comparisons. Their width reflects uncertainty in the estimated group contrast, not a probability that any particular value is correct.

In general, precision depends on factors including the number of participants, the number of observed events, and the variability of the outcome. Here, the primary counts are 19 participants with the event in the DAR-901 group and 18 in the placebo group. The registry record does not provide additional information on missingness or analysis populations that would allow a more complete account of the precision. The confidence intervals should therefore be read as estimates of statistical uncertainty under the posted comparison, not as a guarantee that all sources of uncertainty have been captured.

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

For the primary endpoint, planning for 100% of the observed effect gives 172,223 participants per arm for 80% power and 230,558 participants per arm for 90% power. Planning for 75% of the observed effect gives 304,810 participants per arm for 80% power and 408,053 participants per arm for 90% power. Planning for 50% of the observed effect gives 682,749 participants per arm for 80% power and 914,006 participants per arm for 90% power.

In plain language, the 80% power column gives the modeled per-arm sample size for a design with an 80% chance of detecting the specified effect under the stated assumptions; the 90% power column does the same for a 90% chance. These are planning illustrations based on the observed effect, not observed power from the completed trial. Smaller effects need more participants to distinguish them from random variation under the same assumptions.

The secondary endpoint has its own planning illustrations. For 100% of its observed effect, the figures are 1,503 participants per arm for 80% power and 2,012 participants per arm for 90% power. For 75%, they are 2,460 and 3,292; for 50%, they are 5,054 and 6,765 participants per arm, respectively. These figures use the same listed planning assumptions and are not the trial’s original sample-size rationale.

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 = 0.058; treatment proportion p₁ = 0.060; average p̄ = 0.059.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3337 = 0.6541.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3337 = 0.2809.
4. n = (0.6541 + 0.2809)² / (0.0023)² = 172,222.9, rounded up to 172,223 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 <- 0.0580645161290323                          # control proportion
p1 <- 0.0603174603174603                          # 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(2712424)
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 = 172,223 (80% power), 230,558 (90% power)
 75% of observed effect: n per arm = 304,810 (80% power), 408,053 (90% power)
 50% of observed effect: n per arm = 682,749 (80% power), 914,006 (90% power)
power.prop.test: 172222.9 
Simulated power at n = 172,223 per arm: 0.804 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary endpoint and one secondary endpoint, but it does not report a statistical plan for handling multiple comparisons. It also lists zero analyses and no reported analyses for the secondary outcome. In general, examining multiple endpoints creates more opportunities for chance findings, so confirmatory interpretation is strongest when the outcome hierarchy and multiplicity strategy are specified in advance. Whether any such strategy was used is not reported in the registry record.

The primary comparison is identified as unadjusted. The record does not describe an adjusted analysis, the covariates considered, or the model used. Nor does it report interim analyses or stopping rules. These details are important for understanding whether repeated looks at accumulating data or additional analyses could have influenced the interpretation. They cannot be inferred from the completed status or from the posted estimates.

The registry record does not state how missing IGRA results were handled, whether participants with incomplete follow-up were included, or how the analysis population was defined. It also does not describe whether the primary results followed an intention-to-treat, per-protocol, or other population definition. The counts and denominators are reported, but they do not reveal the reasons any participant may have been excluded from an analysis or lacked an evaluable test.

In general, missing outcome information can affect a group comparison if the chance of an outcome being observed differs across groups or is related to the outcome itself. The extent and direction of any such effect depend on information about missingness and the analysis method. Since those details are not reported in the registry record, the results cannot be evaluated for sensitivity to missing-data assumptions.

These omissions do not invalidate the posted counts, but they narrow the audit trail available to readers. A fuller account would ordinarily clarify the planned outcome hierarchy, analysis populations, methods for incomplete observations, and any interim or adjusted analyses. Without that information, the most defensible reading is limited to the posted unadjusted comparisons and their stated uncertainty.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: tuberculosis (1.0%), cellulitis (0.3%), tonsillitis (0.3%), urinary tract infection (0.3%), hiv infection (0.3%).

The serious adverse event summary lists 6 affected participants among 315 at risk in the DAR-901 group and 3 among 310 at risk in the placebo group. The record lists zero deaths in each group. These are counts of participants affected, not a comparison adjusted for follow-up duration or other factors. No such adjusted safety analysis is reported in the registry record.

For other adverse events, the record lists 126 affected participants among 315 at risk in the DAR-901 group and 142 among 310 at risk in the placebo group. These figures are separate from the serious adverse event counts and should not be added to them; the registry record does not explain whether participants could appear in both categories.

The listed serious event terms include Tuberculosis at 1.0%, and Cellulitis, Tonsillitis, Urinary tract infection, and HIV infection at 0.3% each. The record does not give arm-specific counts for those terms in the listed summary. These figures describe reported events in this trial; by themselves they do not establish that an event was caused by the intervention or that the groups differ in safety. The registry record does not provide further detail about severity, timing, attribution, or statistical comparison.

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

The primary result describes the difference observed between the randomized groups in recorded IGRA conversion during the stated 3-year timeframe. The event counts were 19 among 315 participants assigned to DAR-901 and 18 among 310 assigned to placebo. The reported risk difference is close to zero, but its confidence interval includes effects in both directions. The posted data therefore do not establish a clear group difference on this endpoint.

This is not the same as showing that the groups are equivalent or proving that the intervention has no effect. A finding that does not distinguish the groups statistically can reflect a genuinely small difference, uncertainty from limited event information, or other features of the data and analysis. The confidence interval shows that the estimate is not precise enough to exclude a range of possible differences.

The endpoint is infection defined through IGRA conversion, not tuberculosis disease. The trial result should not be extended to outcomes that the registry record does not report, or to populations, schedules, or settings beyond the registered trial description. The record describes adolescents in Tanzania who previously received BCG, and it reports a 3-year timeframe. Wider generalization requires evidence beyond these posted results.

Safety counts are also descriptive. The recorded serious adverse events and deaths provide useful information about what was reported during the study, but the registry record does not provide an adjusted safety comparison or attribution details. The counts alone do not establish causation or settle whether the intervention changed risk.

In general, trial results are most informative when interpreted with their design, outcome definitions, uncertainty intervals, and analysis details. Here, important analytic details—including missing-data handling, analysis populations, and multiplicity plans—are not reported in the registry record. The posted evidence supports a cautious description of the observed outcomes, rather than a broad claim about benefit, absence of effect, or safety.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it illustrates the difference between a point estimate and the uncertainty around it. The primary estimate is close to zero, but the confidence interval spans negative and positive differences. A reader who focuses only on the near-zero estimate may overstate how precisely the underlying effect is known; a reader who focuses only on the p-value may miss the range of effects compatible with the data.

The trial also makes the role of event counts visible. The primary comparison is based on 19 events in one group and 18 in the other. In general, a binary outcome with relatively few events can yield wide uncertainty even when the total enrollment is several hundred. The count of participants enrolled does not by itself determine the precision of an outcome comparison; how many events occur also matters.

Its secondary endpoint illustrates why outcome definitions and multiplicity matter. A secondary measure can have a different numerical pattern without providing decisive evidence, especially when the record does not report a hierarchy or adjustment plan. Statistical interpretation requires attention to the family of questions asked, not just to an individual comparison.

Finally, the record demonstrates the importance of transparent analysis reporting. Randomization and a placebo comparator describe key design features, while the lack of posted details on missing data, analysis populations, and interim procedures limits independent assessment of the analysis. Together, these features show why effect estimates, precision, and reporting completeness should be considered alongside each other.

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 outcome is defined by conversion from a negative to a positive IGRA result, but the registry record does not describe test timing, confirmation requirements, or handling of indeterminate results. Those details could affect how the endpoint was classified. The record also does not report how missing or incomplete IGRA observations were managed, making it difficult to assess the impact of unavailable outcome data.

The posted primary comparison is unadjusted, and the registry record does not provide a statistical model, adjusted estimates, or the covariates considered. It does not describe the analysis population or explain how the reported denominators relate to randomization, follow-up, and outcome availability. The record lists an enrollment of 625, while outcome group sizes are 315 and 310; it does not give additional participant-flow details.

The registry record does not report the original sample-size justification, interim analysis procedures, or a multiplicity plan. It lists zero analyses and no reported secondary analyses. As a result, readers cannot compare the posted results with a detailed prespecified statistical plan or determine whether additional analytic choices affected interpretation.

The structured masking entry is quadruple, while the official title describes the study as double-blind. The record does not clarify who was masked or report whether masking was maintained. The safety summary provides affected-participant counts and selected serious event terms, but it does not provide detailed timing, attribution, or adjusted comparisons.

These limitations are specific gaps in the registry record; they do not show that the trial failed to use particular procedures. They constrain what can be verified from the posted information and should be kept in mind when interpreting the estimated effects and safety counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: DAR-901 TB Booster Vaccine to Prevent TB in Adolescents — NCT02712424.
• Registry record last updated 2021-05-11; status last verified 2021-04.
• Results first posted 2021-05-11.
• 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

NCT02712424 is a completed phase 2 randomized, placebo-controlled, parallel-group trial of DAR-901 in adolescents who had previously received BCG. The registry record lists an enrollment of 625 and describes intradermal DAR-901 and sterile saline placebo injections. The official title calls the study double-blind, while the structured masking entry is quadruple.

The primary endpoint was new Mycobacterium tuberculosis infection based on IGRA conversion from negative to positive over 3 years. The comparison was unadjusted, with 19 events among 315 participants in the DAR-901 group and 18 among 310 in the placebo group. Its risk-difference confidence interval includes zero. Persistent new infection was listed as a secondary endpoint.

The record lists zero analyses and does not report the original sample-size rationale, interim analysis plan, multiplicity approach, missing-data methods, or analysis populations. Safety summaries include serious and other adverse event counts and zero deaths in both groups. These results describe the posted outcomes; important details needed for a fuller assessment are not reported in the registry record.