Factor Xa Inhibitor, PRT054021, Against Enoxaparin for the Prevention of Venous Thromboembolic Events (EXPERT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Factor Xa Inhibitor, PRT054021, Against Enoxaparin for the Prevention of Venous Thromboembolic Events (EXPERT) (NCT00375609), a randomized phase 2 study. The primary outcome is Incidence of Adjudicated Venous Thromboembolism (VTE).

2. Clinical Question

3. Trial Design

EXPERT was a phase 2, randomized, parallel-group trial of prevention of venous thromboembolic events after unilateral total knee replacement. The registry lists enrollment as 215 and the study status as completed. The study began in 2006-05, with primary completion in 2007-01. Portola Pharmaceuticals is listed as the sponsor. The registry record does not report the original sample-size justification or the detailed randomization procedure.

The study compared three regimens: betrixaban 15 mg orally twice daily, betrixaban 40 mg orally twice daily, and enoxaparin 30 mg subcutaneously every 12 hours. Each regimen was described as lasting 10 to 14 days. The masking field is none, indicating an open-label design in the registry. The record does not report whether endpoint adjudicators were masked to treatment assignment.

The primary endpoint was the incidence of adjudicated VTE through Day 10-14 following surgery, assessed at the mandatory venogram. The analysis population was defined as randomized patients who took at least one dose after randomization and had an evaluable venogram. The reported measure is the percentage of participants with an event, accompanied by a 95% confidence interval.

The registry also lists a secondary endpoint concerning pulmonary embolism and all deep vein thrombosis, proximal and distal, assessed at follow-up at approximately 6 (±2) weeks after surgery. It does not post a reported statistical analysis for that endpoint. Details of the allocation ratio, inclusion and exclusion criteria, handling of protocol deviations, and prespecified analysis 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.

Before assignment: Patients scheduled to undergo elective primary unilateral total knee replacement (TKR) surgery were evaluated for eligibility 1 to 30 days before surgery (Screening). Consenting subjects who remained eligible for the study after TKR were randomized. 215 patients were randomized and all but 1 received at least 1 dose of study drug.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized patients who took at least 1 dose of study medication after randomization and for whom an evaluable venogram was available

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.

Population: All randomized patients who took at least 1 dose of study medication after randomization.

6. Primary Endpoint

The registry lists the primary outcome as Incidence of Adjudicated Venous Thromboembolism (VTE), measured over Through Day 10-14 following TKR surgery, at time of mandatory venogram.

The primary endpoint is the incidence of adjudicated venous thromboembolism through Day 10-14 following total knee replacement, measured at the time of the mandatory venogram. An event is defined as deep vein thrombosis, proximal and/or distal, and/or pulmonary embolism. The registry reports the endpoint as the percentage of participants with an event, with a 95% confidence interval for each group.

This endpoint combines clinically relevant types of venous thrombosis under a prespecified definition, while the mandatory venogram provides a planned assessment for deep vein thrombosis. The registry also describes daily monitoring during hospitalization and contact every 2 to 4 days after discharge, before the venogram, to monitor for study endpoints. These details help explain how events were sought during the period leading to the primary assessment; they do not establish that every event was detected.

The analysis population is narrower than all randomized participants: it includes people who took at least one dose of study medication after randomization and had an evaluable venogram. Thus, the reported percentages describe this defined population rather than necessarily representing every person randomized. The registry record does not report the number of participants excluded from this endpoint population or the reasons for any missing venograms.

7. Results Posted in the Registry

• Betrixaban 40 mg: 15.4% (10/65) versus 20.0% (14/70) on control; risk difference -4.6 percentage points (95% CI -17.5 to 8.2), risk ratio 0.77 (0.37–1.61); unadjusted two-proportion z-test p = 0.483.
• Enoxaparin: 10.0% (4/40) versus 20.0% (14/70) on control; risk difference -10.0 percentage points (95% CI -23.2 to 3.2), risk ratio 0.50 (0.18–1.42); unadjusted two-proportion z-test p = 0.173.

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.

Incidence of Adjudicated Pulmonary Embolism (PE) and All Deep Vein Thrombosis (DVT) (Proximal and Distal)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Betrixaban 40 mg: 15.4% (10/65) versus 20.0% (14/70) on control; risk difference -4.6 percentage points (95% CI -17.5 to 8.2), risk ratio 0.77 (0.37–1.61); unadjusted two-proportion z-test p = 0.483.
  • Enoxaparin: 12.5% (5/40) versus 20.0% (14/70) on control; risk difference -7.5 percentage points (95% CI -21.4 to 6.4), risk ratio 0.62 (0.24–1.61); unadjusted two-proportion z-test p = 0.317.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Betrixaban 40 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enoxaparin and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a secondary outcome concerning adjudicated pulmonary embolism and all deep vein thrombosis, proximal and distal, assessed at follow-up at approximately 6 (±2) weeks after surgery. The event percentages across the groups follow a broadly similar pattern to the primary endpoint, with betrixaban 15 mg having the highest reported percentage and enoxaparin the lowest, while betrixaban 40 mg lies between them. This describes the direction of the posted group estimates, not evidence of a reliable treatment difference.

The secondary outcome is related to the primary result because both concern venous thromboembolism after knee replacement, but the timing differs. The primary assessment is through Day 10-14 at the mandatory venogram; the secondary assessment is at the later follow-up. A pattern that appears similar across these assessment times can be informative descriptively, but it does not make the outcomes interchangeable. Differences in timing and endpoint definition can affect what events are captured.

The registry reports no analyses for the secondary endpoint. The simple recalculations therefore do not have the status of a registry-reported adjusted analysis, and the record does not describe a prespecified inferential plan for these comparisons. Unadjusted secondary results carry less weight because multiple outcomes or comparisons can increase the chance of observing an apparently notable result by chance, especially when no multiplicity strategy is reported. They are most appropriately treated as exploratory context alongside the primary result, rather than as independent confirmation.

The registry does not report whether the secondary endpoint was designated in advance for confirmatory testing, how missing follow-up information was handled, or whether secondary comparisons were included in a formal hierarchy. Those omissions limit the strength of conclusions that can be drawn from the secondary pattern.

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

• Incidence of Adjudicated Pulmonary Embolism (PE) and All Deep Vein Thrombosis (DVT) (Proximal and Distal)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each person either met the adjudicated VTE definition during the assessment period or did not. A percentage is a natural summary for a binary outcome because it communicates the share of the analyzed group with an event. The primary outcome definition includes deep vein thrombosis, proximal and/or distal, and/or pulmonary embolism. The registry’s endpoint population requires at least one post-randomization dose and an evaluable venogram.

What does a confidence interval express?

A confidence interval describes uncertainty in an estimate. For an event percentage, the interval gives a range of values compatible with the observed data under the interval method’s assumptions. It is not a guarantee that the true value lies within the interval, and it does not indicate how likely an individual participant is to experience an event. Wider intervals indicate less precision than narrower intervals. The posted percentages and their 95% confidence intervals should be considered together: the point estimate is the central estimate, while the interval shows how uncertain that estimate is.

How should the risk difference be read?

A risk difference compares two event proportions by subtracting the reference-group proportion from the comparison-group proportion. A negative value means the observed proportion in the comparison group is lower than in the reference group; a positive value means it is higher. The recalculated values are unadjusted comparisons derived from the posted group summaries. They are not adjusted for participant characteristics or other factors. The confidence interval around a risk difference indicates the range of differences compatible with the data under the calculation’s assumptions. If that interval includes zero, the data are compatible with no difference as well as with values on either side of zero.

What does the p-value contribute?

An unadjusted p-value describes how unusual the observed data, or data more extreme, would be under a statistical model in which there is no difference between groups. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. It is also not a substitute for the confidence interval: the interval communicates a range of plausible effect sizes, while the p-value addresses compatibility with a specified null model. The posted p-values are unadjusted recalculations, so they do not account for multiple comparisons.

Why can a small trial have uncertain estimates?

When relatively few participants contribute to an outcome, the observed proportion can change noticeably with only a small change in the number of events. That sampling variability is reflected in wider confidence intervals. A randomized design can support a fair comparison in principle, but randomization does not remove uncertainty from a modest amount of outcome information. The registry does not report the original sample-size justification, the planned power, or the statistical assumptions used to design the trial.

How should the recalculations be understood?

The pairwise risk differences, confidence intervals, and p-values are simple unadjusted recalculations from the posted summary statistics. They are not a substitute for a sponsor-reported analysis, and the registry record reports no analyses for these comparisons. The record does not identify a covariate-adjusted model, a stratification approach, or a method for handling missing outcome data. Accordingly, interpretation should stay close to the observed group percentages and the uncertainty around the unadjusted contrasts rather than implying a more elaborate analysis than the record documents.

Why does the binary outcome definition matter?

A combined endpoint can capture more than one kind of event, but it also means the overall percentage does not indicate how much each event type contributed. The registry lists pulmonary embolism and deep vein thrombosis as a secondary outcome at follow-up, but does not post a reported analysis separating the primary endpoint into components. The primary result therefore addresses the combined VTE definition as recorded, not the individual contribution of each component. The event-adjudication process is named, but procedural details, criteria for adjudication, and masking of adjudicators are not reported in the registry record.

11. Confidence Intervals and Precision

The primary event percentages have 95% confidence intervals that are relatively broad: 11.4 to 31.3 for betrixaban 15 mg, 7.6 to 26.5 for betrixaban 40 mg, and 2.8 to 23.7 for enoxaparin. Each interval includes a range of event percentages, rather than supporting a narrowly defined estimate. The interval widths reflect uncertainty in the group-specific estimates; they should not be interpreted as ranges containing most individual participants’ outcomes.

The recalculated risk-difference interval for betrixaban 40 mg versus betrixaban 15 mg runs from -0.174 to 0.082. For enoxaparin versus betrixaban 15 mg, it runs from -0.232 to 0.032. Both intervals include zero and extend to values on both sides of it. Thus, the posted estimates do not precisely determine whether the comparison groups differ, or how large a difference might be. The intervals also include a range of effect sizes, so a point estimate alone would give an incomplete account of the evidence.

Confidence intervals are useful for understanding precision, but their interpretation depends on the statistical method and the population analyzed. The registry identifies the intervals as 95% confidence intervals but does not describe the method used to construct them. The analysis population requires an evaluable venogram, and the registry does not report how missing or unevaluable assessments were handled. The available precision assessment therefore concerns the posted estimates and cannot resolve uncertainty about participants who were not represented in the endpoint analysis.

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 illustrations based on the observed effect, not the trial’s own design assumptions. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning exercise considers detecting the stated fraction of the observed effect. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

Each planning figure is the number of participants per arm for the comparison being considered; these are not total sample sizes. The 80% power column describes a planning target in which a study designed under the stated assumptions would have an 80% chance of detecting the specified effect if that effect were real. The 90% power column uses a higher target chance of detection. These are design calculations, not descriptions of the probability that the observed trial result is correct.

Rows for planning for 100% of the observed effect use the full observed difference as the target effect. Rows for planning for 75% or 50% of the observed effect use smaller target effects. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same planning assumptions. The displayed numbers are therefore sensitive to the effect size chosen for planning. They should not be read as evidence that the trial had a particular probability of detecting its observed result: this is not observed power.

Because the calculations use the observed effect as their starting point, they are illustrative rather than a reconstruction of the protocol’s design process. The registry record does not report the trial’s original target effect, intended power, or planned allocation assumptions.

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 = 0.200; treatment proportion p₁ = 0.154; average p̄ = 0.177.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5397 = 1.0577.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5387 = 0.4534.
4. n = (1.0577 + 0.4534)² / (-0.0462)² = 1,071.9, rounded up to 1,072 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 <- 0.2                          # control proportion
p1 <- 0.153846153846154                          # 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(375609)
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 = 1,072 (80% power), 1,435 (90% power)
 75% of observed effect: n per arm = 1,955 (80% power), 2,617 (90% power)
 50% of observed effect: n per arm = 4,508 (80% power), 6,034 (90% power)
power.prop.test: 1071.9 
Simulated power at n = 1,072 per arm: 0.803 (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 lists a primary VTE endpoint and a secondary outcome concerning pulmonary embolism and deep vein thrombosis at follow-up. The results include more than one treatment comparison, and the study has more than one outcome. Testing multiple comparisons or outcomes can increase the chance that at least one result appears notable by chance. The registry record does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a prespecified strategy for interpreting secondary analyses. The unadjusted p-values should therefore not be treated as if they were adjusted for the full set of possible comparisons.

The registry record reports no analyses for the listed secondary endpoint. It also does not report a detailed statistical analysis plan, whether analyses were prespecified, whether interim analyses took place, or which analysis populations were used beyond the primary endpoint’s stated population. The original sample-size justification and any planned handling of missing data are not reported in the registry record.

For the primary outcome, the stated population includes randomized patients who took at least one dose after randomization and had an evaluable venogram. This is a defined, treated-and-evaluable population rather than a clear statement that all randomized participants were included in the primary analysis. The record does not provide the number or characteristics of participants without an evaluable venogram, reasons for missing assessments, or an imputation or sensitivity-analysis approach. It also does not explain how participants who discontinued treatment or deviated from the regimen were handled.

These reporting gaps matter because missing outcome information and analysis-population choices can influence estimates. The available results support interpretation of the reported evaluable-population percentages and simple unadjusted comparisons, but they do not allow assessment of the robustness of the findings to alternative missing-data assumptions or analysis populations.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: arthralgia (2.3%), arthritis bacterial (1.2%), cellulitis (1.2%), procedural pain (1.2%), atrial fibrillation (1.2%).

The serious adverse event figures are reported separately from the primary efficacy population. The registry lists 3 serious adverse events among 87 participants at risk in the betrixaban 15 mg group, 6 among 84 at risk in the betrixaban 40 mg group, and 1 among 43 at risk in the enoxaparin group. These are descriptive counts within the reported safety groups; they are not adjusted comparisons and do not, by themselves, establish a difference in safety between regimens.

The registry also lists serious adverse event terms and percentages, including arthralgia at 2.3%, and arthritis bacterial, cellulitis, procedural pain, atrial fibrillation, and hiatus hernia at 1.2% each. These entries describe events recorded in the registry, not necessarily all possible harms or the causal relationship of an event to study medication. The deaths field is not populated; deaths are not reported in the registry record. The record does not provide enough detail to compare severity, timing, duration, or treatment relatedness across groups.

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

The posted primary results describe the observed percentage of participants with adjudicated VTE in each treatment group within the defined endpoint population. The group estimates differ numerically, and the recalculated unadjusted risk differences point below zero for both comparisons with betrixaban 15 mg. However, both risk-difference confidence intervals include zero, and the intervals cover values on either side of it. The estimates are not precise enough to establish the direction or magnitude of a difference with confidence.

A p-value that does not meet a conventional threshold is not proof that treatments are equivalent, and a numerical difference in observed percentages is not proof of a treatment effect. Equivalence or non-inferiority would require a suitable prespecified margin and analysis; such information is not reported in the registry record. The posted data also do not establish that one regimen works or does not work. They describe event estimates and their uncertainty in this trial.

The findings apply to the endpoint and population defined in the record: randomized participants who took at least one dose after randomization and had an evaluable venogram. The registry does not provide enough information to determine how missing venograms may affect interpretation or how representative the analysis population is of other patient groups. The open-label design and lack of reported detail about masking of adjudicators are additional considerations when interpreting an endpoint based on adjudication.

The secondary outcome offers later follow-up context, but no registry-reported analyses are posted for it. It cannot be treated as confirmatory evidence. The trial is phase 2, and the record does not report the original sample-size justification or a full statistical analysis plan. Taken together, the results are best viewed as estimates from a randomized comparison that remain uncertain, rather than as definitive evidence about comparative effects.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between a randomized comparison and a precise estimate. Random allocation can help make treatment groups comparable in expectation, but it does not guarantee narrow confidence intervals. The posted group estimates and risk-difference intervals show why effect size and uncertainty must be read together: a point estimate alone can conceal a broad range of values compatible with the data.

The endpoint also highlights how population definitions shape interpretation. The primary result is not simply a percentage among everyone randomized; the registry defines the analysis population by treatment exposure and an evaluable venogram. Those conditions are relevant to understanding who contributes to the estimate, and missing endpoint information can affect how broadly the result applies.

EXPERT also demonstrates the importance of distinguishing reported analyses from recalculations. The pairwise comparisons are simple unadjusted calculations from posted summary statistics, while the registry reports no analyses for the secondary outcome. Without a reported analysis plan, multiplicity strategy, and missing-data approach, readers have limited grounds for interpreting the comparisons as confirmatory.

Finally, planning illustrations derived from observed effects should not be confused with the trial’s original design or with observed power. Their value is in showing how the participant requirement changes when the target effect changes under stated assumptions. The original planning rationale is not reported in the registry record, so the illustrations cannot explain why this trial enrolled its recorded number of participants.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves important design and analysis details unavailable. It does not report the eligibility criteria in sufficient detail to assess how closely the analyzed participants represent broader populations undergoing total knee replacement. It also does not report the allocation ratio or detailed procedures used to generate and conceal randomization. Although masking is listed as none, details about whether event adjudicators knew treatment assignment are not reported.

The primary endpoint depends on an evaluable mandatory venogram, but the record does not report the number of missing or unevaluable venograms, the reasons for missingness, or how those participants were handled. The stated analysis population also requires at least one post-randomization dose, so it does not establish that all randomized participants contributed to the primary estimate. The record does not report a sensitivity analysis for alternative missing-data assumptions or analysis populations.

The registry provides no detailed statistical analysis plan, original sample-size justification, or reported analyses for the secondary outcome. It does not indicate whether interim analyses occurred, how multiplicity was addressed, or whether the pairwise comparisons were prespecified. These omissions limit evaluation of the inferential framework and the robustness of the results.

The trial is phase 2 and open-label, and the reported group confidence intervals are broad. The results therefore have limited precision and should not be taken as definitive evidence of comparative effects. The adverse event record is also incomplete for some interpretation: deaths are not reported in the registry record, and the relationship of listed events to treatment is not established by the counts alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Factor Xa Inhibitor, PRT054021, Against Enoxaparin for the Prevention of Venous Thromboembolic Events (EXPERT) — NCT00375609.
• Registry record last updated 2023-08-07; status last verified 2023-08.
• Results first posted 2017-12-15.
• 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

EXPERT was a completed, randomized, open-label, parallel-group phase 2 study of prevention of VTE after unilateral total knee replacement. The registry lists enrollment as 215 and Portola Pharmaceuticals as sponsor. It compared betrixaban 15 mg and 40 mg twice daily with enoxaparin 30 mg every 12 hours, each described for 10 to 14 days.

The primary endpoint was adjudicated VTE through Day 10-14 following surgery, assessed at the mandatory venogram. The reported percentages were 20.0 for betrixaban 15 mg, 15.4 for betrixaban 40 mg, and 10.0 for enoxaparin. The recalculated unadjusted risk-difference intervals include zero. The registry record does not report a full statistical analysis plan, the original sample-size justification, or analyses for the listed secondary outcome.