Medication Treatment for Opioid Use Disorder in Expectant Mothers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Medication Treatment for Opioid Use Disorder in Expectant Mothers (NCT03918850), a randomized phase 3 study. The primary outcome is Percentage of Illicit Opioid-negative Urine Samples During Pregnancy.

2. Clinical Question

In practical statistical terms, the comparison asks whether the trial data are compatible with BUP-XR having no clinically unacceptable disadvantage on the pregnancy urine outcome, under a prespecified margin. A difference in observed averages alone cannot answer that question: the margin, analysis method, and uncertainty around the contrast all matter. The registry record reports arm-level averages and an unadjusted recalculation of the mean difference and confidence interval from those summaries. It does not report a sponsor analysis for the primary outcome. The posted numbers therefore describe the observed data and an unadjusted comparison, rather than a complete formal non-inferiority assessment.

3. Trial Design

The registry identifies this as a phase 3 randomized, open-label, parallel-group trial of extended-release and daily sublingual buprenorphine formulations for opioid use disorder in pregnancy. Enrollment was 140. The registry lists the study as completed, with a start date of 2020-07-21 and primary completion date of 2025-01-31. The sponsor is listed as T. John Winhusen, PhD.

Participants were assigned to BUP-XR or BUP-SL. The trial was unmasked, so participants and study personnel were not blinded according to the registry record. The BUP-XR regimen was weekly subcutaneous injection during pregnancy; postpartum treatment depended on breastfeeding status. BUP-SL was daily sublingual buprenorphine, with or without naloxone according to site preference, during pregnancy and postpartum. The target BUP-SL dose was 16 mg daily, but the prescribing clinician could determine a lower or higher actual dose.

The primary endpoint covered screening through delivery. Since randomization occurred over a range of gestational ages, the time available for pregnancy assessments varied; the registry describes this as an average of 10-34 weeks. Weekly urine samples were shipped to a central laboratory to test for illicit opioids and/or metabolites. Postpartum outcomes were assessed from delivery through 12 months postpartum.

The registry record does not report the original sample-size justification, the prespecified analysis model, the non-inferiority margin, or the planned handling of missing data. It lists no reported analyses. Those omissions matter when interpreting whether the posted summary statistics answer the trial’s stated non-inferiority question.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Illicit Opioid-negative Urine Samples During Pregnancy, measured over From screening (at 6-30 weeks estimated gestational age) to delivery, an average of 10-34 weeks.

The primary endpoint is the percentage of illicit opioid-negative urine samples during pregnancy. Weekly samples were shipped to a central laboratory for analysis for illicit opioids and/or their metabolites. The assessment period ran from screening, at 6-30 weeks estimated gestational age, to delivery, an average of 10-34 weeks. Because participants entered the trial at different gestational ages, the number of scheduled urine assessments varied among participants.

This endpoint summarizes test results across the pregnancy assessment period. It is not the percentage of participants who were opioid-negative, nor does it establish that a participant had no illicit opioid use throughout pregnancy. A participant’s result can reflect more than one urine assessment, and the registry description does not state how missing or unusable samples were handled in the endpoint calculation.

Urine testing provides an objective laboratory measure of detected illicit opioids or metabolites at the times samples are collected. It is relevant to the trial’s stated objective of comparing illicit opioid use between treatment groups. However, the registry record does not describe the primary analysis model, how repeated samples were accounted for, or a non-inferiority margin. Those details are needed to interpret the endpoint in the context of the formal trial hypothesis, beyond comparing the posted group averages.

7. Results Posted in the Registry

• BUP-SL: mean 72.60 versus 82.50 on control; difference -9.90 (95% CI -21.54 to 1.74), standardized effect d = -0.28; z-test p = 0.096.

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.

Percentage of Illicit Opioid-negative Urine Samples Postpartum

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • BUP-SL: mean 59.50 versus 60.20 on control; difference -0.70 (95% CI -12.20 to 10.80), standardized effect d = -0.02; z-test p = 0.905.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BUP-SL and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Days With Study Medication Adherence During Pregnancy

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • BUP-SL: mean 84.90 versus 84.40 on control; difference 0.50 (95% CI -7.96 to 8.96), standardized effect d = 0.02; z-test p = 0.908.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BUP-SL and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Days With Study Medication Adherence - Postpartum

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • BUP-SL: mean 75.50 versus 69.30 on control; difference 6.20 (95% CI -5.58 to 17.98), standardized effect d = 0.18; z-test p = 0.302.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BUP-SL and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists 17 secondary outcomes, including postpartum urine results, medication adherence, drug and alcohol urine results, craving, and prenatal care utilization. It lists no reported analyses. The detailed arm summaries available for postpartum illicit opioid-negative samples and medication adherence during and after pregnancy give a mixed descriptive pattern: the group averages are close for some outcomes, while postpartum adherence has a numerical difference. These summaries do not establish consistent advantage for either formulation across all secondary measures.

For the detailed secondary comparisons, the unadjusted recalculated confidence intervals include zero. Read together, these results do not provide a clear separation between group means in those summary-based comparisons. They also do not validate or overturn the primary result: secondary outcomes measure different aspects of treatment and follow-up, and postpartum outcomes cover a different period from the pregnancy primary endpoint.

Unadjusted secondary results carry less weight when many outcomes are examined. As a general statistical issue, testing multiple outcomes increases the chance that some estimates appear notable by chance, even when no adjustment is made. The registry record does not report a multiplicity strategy, a hierarchy of secondary hypotheses, or formal sponsor analyses. Therefore, secondary averages and unadjusted p-values are best treated as exploratory descriptions rather than independent confirmatory evidence.

The scope of what can be inferred is also limited by the missing analysis details. The registry does not report the handling of missing postpartum data, analysis populations, or methods for repeated observations. The secondary summaries can describe the posted averages, but they cannot resolve those uncertainties or establish effects on all listed outcomes.

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

• Percentage of Illicit Opioid-negative Urine Samples Postpartum
• Percentage of Days With Study Medication Adherence During Pregnancy
• Percentage of Days With Study Medication Adherence - Postpartum
• Percentage of Drug and Alcohol-negative Urine Samples During Pregnancy
• Percentage of Drug and Alcohol-negative Urine Samples - Postpartum Phase
• Opioid Craving Scale - Pregnancy
• Opioid Craving Scale - Postpartum
• Adequacy of Prenatal Care Utilization Index

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a percentage summarized as a mean for each treatment group. The registry reports standard errors alongside the means. A standard error describes the precision of an estimated mean, rather than the spread of individual participant outcomes. Confusing standard error with standard deviation can make the data appear less variable than they are at the participant level.

What does the mean difference represent?

The recalculated contrast is BUP-SL minus BUP-XR. The reported estimate of -9.9 is therefore the BUP-SL mean minus the BUP-XR mean. A negative value indicates a lower posted average in BUP-SL under that subtraction order. The contrast is an unadjusted calculation from the posted summary statistics; it is not a reported adjusted model estimate. No covariate adjustment or repeated-measures method is described in the registry record.

How should the confidence interval be read?

A confidence interval expresses uncertainty around an estimated contrast. In general, a wider interval indicates less precision, while a narrower one indicates more precision. For the primary recalculation, the interval runs from -21.54 to 1.742. Because it includes zero, the posted summaries do not clearly rule out no mean difference in an unadjusted comparison. The interval does not establish that the treatment effects are equivalent, and the registry record does not give a non-inferiority margin against which to assess its limits.

Why does non-inferiority need a margin?

Non-inferiority is not established simply because a difference is not statistically significant. The trial must define in advance how much disadvantage would still count as acceptably small, then assess whether the data exclude a disadvantage beyond that margin. The registry states the non-inferiority hypothesis but does not report the margin or the planned analysis. Without them, the formal hypothesis cannot be evaluated from the posted unadjusted comparison alone.

What is the role of the p-value?

The unadjusted p-value for the primary recalculation is 0.096. In general, a p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. A p-value also does not substitute for the non-inferiority margin and analysis required by the stated trial question.

Why do repeated urine assessments matter?

The primary outcome aggregates weekly urine assessments, and the number scheduled varied because participants were randomized at different gestational ages. Repeated measurements from the same participant may be related rather than independent. In general, analyses of repeated data should account for that relationship and should specify how participants with different numbers of assessments contribute. The registry describes the testing schedule but does not report the model, weighting approach, or handling of missing samples. As a result, the recalculation from group summaries cannot address those design and analysis details.

What does randomization contribute?

Random assignment is intended to make treatment groups comparable, on average, with respect to measured and unmeasured characteristics at the start of a trial. It supports causal comparisons when allocation, follow-up, and analysis are handled appropriately. This study was open-label, so treatment assignment was not masked. The objective laboratory testing may reduce some subjectivity in classifying urine results, but the registry record does not describe protections against other sources of bias or the analysis population used.

The displayed mean differences and confidence intervals are unadjusted recalculations from posted summaries. The registry record lists no reported analyses, so these calculations should not be mistaken for a sponsor-reported model or the prespecified trial analysis. The original statistical plan, analysis populations, missing-data procedures, and multiplicity approach are not reported in the registry record.

11. Confidence Intervals and Precision

The primary unadjusted recalculated mean difference is -9.9, with a confidence interval from -21.54 to 1.742. This range captures substantial uncertainty around the contrast: the posted data are compatible with a considerably lower average in BUP-SL and also with a small average in the opposite direction. The interval includes zero, so the recalculation does not clearly distinguish the group means in an unadjusted comparison.

Precision should be interpreted in relation to the trial question. A confidence interval for a difference can help show which contrasts remain compatible with the data, but a non-inferiority decision also needs the prespecified margin. That margin is not reported in the registry record. Without it, the interval cannot be classified as excluding or permitting an unacceptable disadvantage under the trial’s planned criterion.

The arm-level standard errors are 4.2 for both pregnancy means. These quantify uncertainty in the estimated means; they are not individual-level standard deviations. The registry reports a varying number of scheduled urine assessments because participants entered at different gestational ages, but it does not report how this variation, within-participant dependence, or missing samples were addressed in a formal analysis. Those features may affect precision estimates, and the summary recalculation cannot account for them.

The recalculated interval is unadjusted and should be read as a summary-based comparison, not as a replacement for a prespecified analysis. No confidence interval from a sponsor-reported primary model is listed in the registry record.

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 illustrations give participants per arm for 80% power and participants per arm for 90% power. They use 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 the stated fraction of the observed effect. These are planning illustrations based on the observed effect, not the trial’s original design justification; the trial’s own design assumptions are not reported in the registry record. This is not observed power.

For the primary pregnancy outcome, planning for 100% of the observed effect gives 198 participants per arm for 80% power and 265 participants per arm for 90% power. Planning for 75% of the observed effect gives 352 participants per arm for 80% power and 471 participants per arm for 90% power. Planning for 50% of the observed effect gives 792 participants per arm for 80% power and 1,060 participants per arm for 90% power.

In plain language, the 80% column describes a planning scenario intended to detect the chosen effect under the listed assumptions with 80% power; the 90% column uses a higher target probability of detecting that effect. Neither is a statement about what this completed trial achieved. The observed difference is modest relative to its uncertainty, so the illustrations require more participants as the target effect becomes smaller. More generally, smaller effects are harder to distinguish from random variation and require more participants under otherwise fixed assumptions.

The displayed numbers are per arm, not combined totals or event counts. They are not a substitute for the original protocol’s sample-size rationale, and their assumptions may not match the actual design or analysis.

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

Worked calculation for this trial

1. Observed difference Δ = -9.900; pooled standard deviation σ = 35.143.
2. n = 2 × (1.96 + 0.842)² × 35.143² / -9.900² = 197.8, rounded up to 198 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 <- -9.90000000000001                      # observed difference in means
sigma <- 35.1433585784557                     # 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(3918850)
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 = 198 (80% power), 265 (90% power)
 75% of observed effect: n per arm = 352 (80% power), 471 (90% power)
 50% of observed effect: n per arm = 792 (80% power), 1,060 (90% power)
power.t.test: 198.8 
Simulated power at n = 198 per arm: 0.795 (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.

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether or how the trial controlled multiplicity across the primary and secondary outcomes. This matters because examining many outcomes can increase the chance of a nominally notable finding through random variation. A prespecified hierarchy, adjustment procedure, or distinction between confirmatory and exploratory outcomes can help readers understand how much weight to place on each result. None is described in the registry record, and no reported analyses are listed.

The record identifies a primary endpoint and states a non-inferiority hypothesis, but it does not report the non-inferiority margin or the formal analysis plan. It also does not report the statistical model, whether the primary analysis was adjusted, or which analysis population was intended. Those omissions prevent a full assessment of whether the reported summaries correspond to the prespecified primary analysis.

Missing-data handling is not reported. This is relevant because urine assessments were scheduled weekly, while the number scheduled varied among participants, and the endpoint was calculated over the pregnancy assessment period. The registry does not state how missed samples, incomplete follow-up, or samples unavailable for testing were handled. Nor does it describe assumptions used to make inference when outcome data were missing.

The registry record also does not report whether repeated urine samples were analyzed with a method that accounts for correlation within participants. A simple comparison of arm means does not reveal whether such dependence was modeled, how participants with different assessment counts were weighted, or whether alternative analyses were conducted.

These are reporting gaps, not evidence that the trial did or did not use a particular method. The posted summaries support a descriptive comparison, but the absent analysis and missing-data details limit interpretation of the formal primary and secondary hypotheses.

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: gestational hypertension (5.6%), pre-eclampsia (4.3%), overdose (4.3%), suicidal ideation (4.2%), weight gain poor (3.0%).

For participants, the registry reports serious adverse events affecting 9 of 69 in BUP-XR and 27 of 71 in BUP-SL. Other adverse events affected 49 of 69 in BUP-XR and 59 of 71 in BUP-SL. The registry reports zero deaths in both participant groups. These are counts of affected participants in the registry’s safety categories; they do not by themselves establish that an event was caused by treatment.

For neonates, serious adverse events affected 9 of 67 in the BUP-XR group and 11 of 70 in the BUP-SL group. The registry reports zero deaths in the BUP-XR neonate group and one in the BUP-SL neonate group. The listed serious event terms include Gestational hypertension at 5.6%, Pre-Eclampsia at 4.3%, Overdose at 4.3%, Suicidal ideation at 4.2%, Weight gain poor at 3.0%, and Pyelonephritis at 2.9%.

Counts should be read alongside the groups at risk and the way events were classified. The registry record does not provide a comparative safety analysis or details that would establish causality. These figures are descriptive safety reports, not a basis for concluding that one treatment has a safer profile.

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

The posted primary summaries show a higher mean percentage of illicit opioid-negative urine samples during pregnancy in BUP-XR than in BUP-SL. The unadjusted recalculated difference is -9.9 when expressed as BUP-SL minus BUP-XR. Its confidence interval includes zero and spans a range of possible differences. The result therefore conveys uncertainty rather than a decisive separation between the group averages.

The finding does not establish non-inferiority. That conclusion depends on a prespecified margin and an analysis designed for the non-inferiority question; the margin and formal analysis are not reported in the registry record. A nonsignificant unadjusted comparison is not proof that treatments are equivalent, and the interval cannot be judged against an unreported threshold.

The endpoint is based on urine samples, not a direct measure of every aspect of opioid use or recovery. The percentage summarizes samples that tested negative during the assessment period; it should not be read as the percentage of participants who remained abstinent. The registry describes variable assessment schedules and does not report how missing samples or repeated measurements were handled in the analysis.

The secondary summaries and safety counts offer additional descriptive information, but the registry lists no reported analyses and does not describe multiplicity procedures. Those results should not be interpreted as definitive evidence across the range of maternal, infant, adherence, and other outcomes.

In short, the posted results describe group averages and their uncertainty, while leaving key elements of the formal trial interpretation unreported. They neither establish equivalence nor support a broad claim that one formulation is better or worse. This statistical summary is not medical advice.

17. Why This Trial Matters Statistically

This trial poses a useful statistical question because the primary hypothesis is explicitly framed as non-inferiority. Non-inferiority questions require more than asking whether a conventional test detects a difference. The acceptable margin must be stated in advance, and the uncertainty around the treatment contrast must be assessed against it. The registry record does not report that margin, illustrating why a stated hypothesis alone is not enough to interpret a posted result as a formal non-inferiority conclusion.

The pregnancy endpoint also involves repeated laboratory measurements over a period that varies with gestational age at randomization. A participant’s urine results are not necessarily independent observations, and participants had different numbers of scheduled assessments. Sound interpretation therefore depends on how repeated measurements and missing samples were handled, but those methods are not reported in the registry record.

Open-label treatment assignment is another feature readers should keep in view. Laboratory urine testing offers an objective component, but masking status and the conduct of follow-up remain relevant to understanding the evidence. The registry identifies the trial as randomized and unmasked but does not describe the detailed analysis protections or populations.

Finally, the posted arm means and recalculated comparison help readers see the direction and uncertainty of the observed primary result. Yet they cannot replace the prespecified analysis or answer unreported questions about multiplicity, missing data, and the trial’s design assumptions. This distinction between descriptive summaries and confirmatory inference is central to reading registry results responsibly.

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.

Several trial-specific reporting gaps constrain interpretation. The registry record does not report the non-inferiority margin, the original sample-size justification, or the primary statistical model. It also lists no reported analyses. Consequently, the unadjusted summary-based comparison cannot be checked against the planned formal analysis or used to determine whether the prespecified non-inferiority criterion was met.

The primary outcome aggregates weekly urine samples, while the number of scheduled assessments varied because randomization occurred across 6-30 weeks estimated gestational age. The registry does not report how variable assessment counts, repeated-measure correlation, missed collections, or unavailable samples were handled. The posted standard errors cannot answer those questions.

The trial was open-label. The urine outcome includes central laboratory testing, but the registry record does not describe whether other steps in outcome collection or analysis were masked, or how potential differences in treatment exposure and follow-up were addressed. The postpartum treatment regimen for BUP-XR also varied by breastfeeding status, while BUP-SL was given during the 12-month postpartum period; the summaries alone do not clarify how those regimen details entered the analysis.

The registry lists numerous secondary outcomes but does not report a multiplicity plan or detailed analyses. The secondary summaries should therefore be interpreted cautiously. Safety counts are descriptive, and the registry does not provide a comparative safety model or establish causal attribution for reported events.

These limitations concern what can be concluded from the registry record; they do not establish that the underlying study failed to address these issues in other materials.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Medication Treatment for Opioid Use Disorder in Expectant Mothers — NCT03918850.
• Registry record last updated 2026-06-04; status last verified 2026-05.
• Results first posted 2026-06-04.
• 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

The MOMs trial, NCT03918850, is listed as a completed phase 3 randomized, open-label, parallel-group study with enrollment of 140. It compared weekly extended-release buprenorphine injection with daily sublingual buprenorphine for opioid use disorder during pregnancy and postpartum.

The primary endpoint was the percentage of illicit opioid-negative urine samples during pregnancy. The posted means were 82.5 for BUP-XR and 72.6 for BUP-SL. The unadjusted recalculated BUP-SL minus BUP-XR difference was -9.9, with a confidence interval from -21.54 to 1.742 and an unadjusted p-value of 0.096.

The registry states a non-inferiority hypothesis but does not report its margin, the original sample-size justification, the formal analysis plan, missing-data methods, or reported analyses. The posted comparison is therefore descriptive and does not establish a formal non-inferiority conclusion.