A Study to Evaluate Efficacy and Safety of VX-150 in Subjects With Acute Pain Following Bunionectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate Efficacy and Safety of VX-150 in Subjects With Acute Pain Following Bunionectomy (NCT03206749), a randomized phase 2 study. The primary outcome is Time-weighted Sum of the Pain Intensity Difference (SPID) Between VX-150 Versus Placebo as Recorded on a Numeric Pain Rating Scale (NPRS) 0 to 24 Hours After the First Dose.

2. Clinical Question

This is a focused comparison of a continuous pain measure over a defined period after dosing. A positive pain-intensity difference was defined by subtracting the post-dose pain score from the baseline score. In the posted results, higher SPID values are described as better scores, and the reported mean for VX-150 was higher than the placebo mean. The comparison is not a direct test against HB/APAP: that arm was included as a reference rather than as a planned statistical comparator.

The question is about the average pain-difference measure during the specified period, not every participant’s response, pain at a single moment, or a broader claim about outcomes outside the recorded measures. The registry record does not report a threshold for a clinically important difference, so the numerical contrast alone does not establish how large a difference would be meaningful to participants.

3. Trial Design

This was a Phase 2, randomized, double-blind, placebo-controlled, three-arm, parallel-design study of VX-150 for acute pain following bunionectomy. The registry lists the masking as quadruple. The interventions were VX-150, HB/APAP, and placebo. The registry record reports enrollment of 243 participants and a completed study.

The study started on 2017-06-29, and the primary completion date was 2017-12-01. Those dates describe the registry’s recorded study timeline; they do not, by themselves, describe the duration of follow-up for each participant. The registry record does not report a more detailed schedule of visits or follow-up in the information available for this analysis.

Randomization and a parallel design mean participants were assigned to study arms, with each participant remaining in an assigned arm rather than crossing between interventions. Double-blind and quadruple-masking labels indicate masking was part of the design, but the registry record does not specify which participant or study roles were masked. Further details of the randomization procedure, allocation concealment, or the trial’s original allocation targets are not reported in the registry record.

The primary endpoint population was the Full Analysis Set, defined as randomized participants who received at least one dose of study drug. The reported primary comparison is between VX-150 and placebo. HB/APAP is identified as a standard-of-care reference arm and was not intended for statistical comparisons with VX-150. The registry record does not report the original sample-size justification or the design assumptions behind the planned enrollment.

The record describes efficacy and safety as study aims, with a pain-intensity endpoint and additional outcomes related to pain relief, rescue medication, and pharmacokinetics. The statistical plan beyond the reported analysis methods, including details of any interim analyses, is not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) included all randomized participants who received at least 1 dose of study drug. As a standard-of-care reference arm, the "HB/APAP" arm was not intended for statistical comparisons to VX-150.

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 Time-weighted Sum of the Pain Intensity Difference (SPID) Between VX-150 Versus Placebo as Recorded on a Numeric Pain Rating Scale (NPRS) 0 to 24 Hours After the First Dose, measured over 0 to 24 hours after the first dose.

The primary endpoint is the time-weighted Sum of the Pain Intensity Difference, or SPID, between VX-150 and placebo on the numeric pain rating scale during 0 to 24 hours after the first dose. Pain intensity difference at a post-dose time point was calculated by subtracting that pain score from the baseline pain score. SPID then combines those differences over time, weighting each by the hours elapsed since the previous measurement.

The pain scale ranges from 0, no pain, to 10, worst possible pain. For SPID24, the registry describes a possible score range from -240, worst score, to 240, best score. A time-weighted measure reflects both the size and duration of recorded pain differences over the assessment period, rather than relying on a single post-dose reading. This can make it useful for comparing the overall pattern of pain scores across a specified time window.

The endpoint is reported as a least-squares mean, with standard error as the dispersion measure. The registry describes the analysis population as randomized participants who received at least one dose. It does not report a clinically important difference threshold for SPID24, so the endpoint’s numerical scale should not be treated as a stand-alone definition of clinical importance.

7. Results Posted in the Registry

• VX-150: mean 36.14 versus 6.64 on control; difference 29.50 (95% CI 15.39 to 43.61), standardized effect d = 0.64; z-test p = <0.001.

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.

Time-weighted Sum of the Pain Intensity Difference Between VX-150 Versus Placebo as Recorded on a NPRS 2 to 24 Hours After the First Dose

• 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:
  • VX-150: mean 34.95 versus 6.43 on control; difference 28.52 (95% CI 15.01 to 42.03), standardized effect d = 0.65; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for VX-150 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time-weighted Sum of the Pain Intensity Difference Between VX-150 Versus Placebo as Recorded on a NPRS 0 to 48 Hours After the First Dose

• 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:
  • VX-150: mean 112.22 versus 49.43 on control; difference 62.79 (95% CI 33.82 to 91.76), standardized effect d = 0.67; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for VX-150 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary pain assessment to other time windows and related measures. The record lists outcomes for SPID during 2 to 24 hours and 0 to 48 hours after the first dose, as well as measures of onset and duration of pain relief, rescue-medication use, and pharmacokinetic concentrations. This broadens the descriptive scope beyond the primary 0 to 24 hour SPID outcome.

The two secondary SPID comparisons with posted numerical results show the same general direction as the primary comparison: the VX-150 group’s reported SPID mean is higher than the placebo group’s in each reported time window, and the sponsor’s ANCOVA comparisons are reported as superiority analyses. They are related measures of pain intensity over overlapping or extended periods, so their agreement in direction is supportive as a pattern within the registry record. They are not independent replications of the primary result because the outcomes involve related measurements from the same study.

Although the record lists eleven secondary outcomes, detailed numerical comparisons are not available for every listed outcome in the information. No conclusion about an unposted or unreported secondary result should be inferred from the listed outcome title alone. The record does not report a multiplicity adjustment or a prespecified hierarchy for secondary testing.

Unadjusted secondary results carry less weight for confirmatory interpretation when multiple outcomes are examined. With repeated testing, some small p-values can arise by chance, and without a reported adjustment or testing hierarchy it is unclear how the secondary findings were protected against that risk. Secondary outcomes can add context and generate hypotheses, but their interpretation should remain distinct from the designated primary analysis.

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

• Time-weighted Sum of the Pain Intensity Difference Between VX-150 Versus Placebo as Recorded on a NPRS 2 to 24 Hours After the First Dose
• Time-weighted Sum of the Pain Intensity Difference Between VX-150 Versus Placebo as Recorded on a NPRS 0 to 48 Hours After the First Dose
• Time to Onset of Perceptible Pain Relief After the First Dose of VX-150 Versus Placebo
• Time to Onset of Meaningful Pain Relief After the First Dose of VX-150 Versus Placebo
• Time to First Rescue Medication After the First Dose of VX-150 Versus Placebo
• Percentage of Participants Using Rescue Medication After the First Dose VX-150 Versus Placebo
• Total Rescue Medication Used After the First Dose of VX-150 Versus Placebo
• Maximum Observed Concentration (Cmax) of VRT- 1207355 (Active Moiety) and VRT- 1268114 (Metabolite M5)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numerical score that can take values across a scale rather than a simple event count. The registry reports group least-squares means and standard errors, followed by an ANCOVA comparison of VX-150 with placebo. ANCOVA, or analysis of covariance, estimates a between-group difference while accounting for covariates specified in the model. Which covariates were used is not reported in the registry record, so the reported adjusted estimate cannot be independently reconstructed from the summaries alone.

What a mean difference describes

A mean difference is the estimated average value in one group minus the estimated average value in the other group, following the comparison’s stated direction. For the primary endpoint, the sponsor reported an LS mean difference of 29.50. The registry’s SPID description identifies higher scores as better scores, and the VX-150 group’s posted mean exceeded the placebo group’s posted mean. The difference summarizes group averages; it does not say that each participant had a change equal to that estimate or that all participants experienced the same pattern.

Why the analysis method matters

The registry’s reported comparison is ANCOVA and is expressed as a least-squares mean difference. Least-squares means are model-based group averages, adjusted according to the model terms. In contrast, the recalculated comparison uses the posted arm summaries to form a simple unadjusted contrast. It is a useful check on the direction and approximate size of the posted result, but it is not the same estimand or procedure as the sponsor’s reported ANCOVA. The record does not give enough information to determine precisely which model choices account for the differences between their estimates and intervals.

The recalculated standard error and confidence interval also rely on assumptions about the variability of the continuous measure. The posted arm dispersion values are standard errors, not standard deviations. The recalculation estimates pooled variability from the reported summary statistics, so its interval is approximate. This is why the recalculated interval should be distinguished from the interval generated by the sponsor’s ANCOVA.

What a p-value does and does not say

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test’s assumptions held. A small p-value is evidence against a zero-difference null in the context of the stated analysis. It is not the probability that the null hypothesis is true, the probability that the result is due to chance, or a measure of the size or clinical importance of an effect. The registry reports an ANCOVA p-value below 0.001 for the primary contrast; the recalculated unadjusted p-value is also < 0.001.

The reported test is a superiority analysis. That classification describes the direction of the statistical question—whether the arms differ in the stated direction under the analysis—not a universal judgment about treatment or outcomes. The estimate and its interval remain important because a p-value alone does not show the range of values compatible with the data.

Why over-dispersion can matter

For count outcomes, over-dispersion means that observed variability exceeds what a simple count model assumes. It can make standard errors too small if the extra variability is ignored. The primary SPID endpoint is continuous, not a count, so count over-dispersion is not the issue for this main comparison. More generally, the choice of model should reflect the outcome’s scale and variability. The registry record does not report enough detail to assess all model diagnostics or assumptions for the ANCOVA.

Analysis populations and missing observations

The primary population is the Full Analysis Set, defined in the record as randomized participants who received at least one dose of study drug. This definition clarifies who was eligible for the primary analysis but does not explain how missing SPID measurements were handled, whether all eligible participants contributed an endpoint value, or how any departures from the analysis population were treated. Those details are not reported in the registry record.

The primary endpoint has a defined post-dose assessment period, but the registry description alone does not reveal the extent or pattern of missing measurements within that period. Missingness can matter when participants with incomplete measurements differ from those with complete measurements. Without a reported missing-data strategy or sensitivity analyses, the effect of missing values on the estimate cannot be assessed from this record.

Multiplicity and secondary analyses

The record lists multiple secondary outcomes, including other time windows for SPID, time to pain relief, rescue-medication measures, and pharmacokinetic measurements. Testing many outcomes creates a multiplicity issue: even when no true effects exist, the chance of at least one apparently unusual result can rise as the number of tests increases. The registry record does not report whether a multiplicity adjustment, hierarchical testing procedure, or other control strategy was used. Secondary p-values therefore should not be treated as if they necessarily had the same confirmatory status as the primary analysis.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. A confidence interval gives a range of values compatible with the data and the analysis assumptions at the stated confidence level. It is not a range containing a fixed proportion of individual participants’ scores, and it does not guarantee that the true value lies within the particular interval.

For the primary comparison, the sponsor’s ANCOVA estimate was 29.50, with a 95% confidence interval from 16.61 to 42.40. This interval is entirely above zero, consistent with the positive difference reported by the model. Its width indicates that the estimate is not known with exact precision: values across the interval remain compatible with the analysis. The recalculated unadjusted interval, 15.39 to 43.61, is wider and is based on a different, approximate procedure.

The two intervals should not be conflated. The sponsor’s interval comes from the reported ANCOVA, while the recalculated interval comes from simple unadjusted calculations using the posted summaries. The registry record does not provide all model details needed to explain the difference in interval width. Neither interval addresses uncertainty from unmeasured outcomes, limitations in the study design, or the possibility that the analysis assumptions are imperfect.

Precision is also distinct from clinical importance. The interval indicates uncertainty around the group difference on the SPID scale; the record does not define a threshold for a clinically important difference. The sample-size planning figures are illustrative calculations from an observed estimate, not a measure of how likely the trial was to detect an effect after it was completed.

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 original design calculation. For this continuous outcome, the entries are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is a stated fraction of the observed effect. The trial’s own original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm under those assumptions for a design with an 80% chance of rejecting the zero-difference null if the assumed effect were the true effect and the model assumptions held. The 90% power column expresses the same planning idea with a higher target probability of detecting that assumed effect. These are hypothetical planning probabilities, not guarantees for an individual study.

The rows consider planning for 100%, 75%, and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect generally requires more participants per arm. The illustrations do not establish what effect is clinically important, and they do not show how the original trial was designed or whether its achieved enrollment was adequate for every endpoint.

This is not observed power. Observed power is not a substitute for interpreting the estimate and its confidence interval after the study; the planning values instead show how sample-size requirements change under stated hypothetical assumptions. The registry record’s original planning rationale is not reported.

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 = 29.500; pooled standard deviation σ = 45.803.
2. n = 2 × (1.96 + 0.842)² × 45.803² / 29.500² = 37.8, rounded up to 38 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 <- 29.5                      # observed difference in means
sigma <- 45.8033007680669                     # 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(3206749)
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 = 38 (80% power), 51 (90% power)
 75% of observed effect: n per arm = 68 (80% power), 91 (90% power)
 50% of observed effect: n per arm = 152 (80% power), 203 (90% power)
power.t.test: 38.8 
Simulated power at n = 38 per arm: 0.788 (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. Analyses Reported by the Sponsor

The sponsor’s primary analysis is an ANCOVA comparison of VX-150 with placebo. It reports an LS mean difference of 29.50 and a 95% confidence interval from 16.61 to 42.40. The recalculation from posted arm summaries gives an unadjusted mean difference of 29.5 and a 95% confidence interval from 15.39 to 43.61. The estimates point in the same direction and are close in magnitude, but the intervals differ.

That distinction is expected when comparing a model-based adjusted estimate with an unadjusted recalculation. The posted arm summaries do not contain all the information needed to reproduce the sponsor’s ANCOVA, including the model covariates. The recalculated result is therefore best read as a simple cross-check, not as an alternative official analysis. The registry record reports the sponsor’s analysis as the trial’s own inferential result.

The sponsor’s p-value is reported as below 0.001, and the recalculated unadjusted p-value is < 0.001. Both express strong statistical evidence against a zero difference under their respective analyses. They do not quantify clinical importance, and the record does not report a threshold for interpreting the SPID difference as clinically important.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple outcomes, time points, or comparisons. Each statistical test has its own chance of producing an apparently unusual result under a null hypothesis. Across many tests, the chance of at least one false-positive finding can increase unless the analysis plan controls or otherwise accounts for this issue. The registry lists a primary endpoint and multiple secondary outcomes, including additional time windows and rescue-medication measures.

The registry record does not report whether the trial used a family-wise error adjustment, a hierarchical testing sequence, a false-discovery approach, or another strategy for multiplicity. It also does not report whether all listed secondary analyses were confirmatory or exploratory. Consequently, the primary analysis can be interpreted as the designated comparison, while secondary results should be considered with the uncertainty created by multiple testing in mind.

The record defines the Full Analysis Set for the primary endpoint as all randomized participants who received at least one dose. It does not report the number of participants with missing primary outcome measurements, the reasons for any missingness, or the method used to handle missing values. It is also not reported whether sensitivity analyses assessed the effect of alternative missing-data assumptions.

These omissions matter because incomplete outcome measurements can affect an estimate if missingness is related to participants’ pain scores or treatment assignment. The available record does not allow readers to determine whether missingness was negligible, balanced, or addressed robustly. The detailed statistical analysis plan, including model covariates and the handling of protocol deviations, is not reported in the registry record.

Interim analyses and any associated stopping rules are also not reported in the registry record. Their absence from the record should not be read as proof that none occurred; it means their presence or absence cannot be established from the information recorded.

16. 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 non-serious adverse event terms

The registry reports serious adverse events for 80 participants at risk in the VX-150 group, 81 in the HB/APAP group, and 82 in the placebo group. It records zero serious adverse events affecting participants in each of these groups. Deaths are also recorded as zero in each group, and no serious adverse-event terms are listed.

These figures describe the serious adverse events recorded in the registry for the stated at-risk groups. They do not establish that serious events are impossible or that no events occurred outside the reported collection or observation period. The registry record does not report the safety follow-up duration or additional detail about ascertainment in the information available for this analysis.

Other adverse events affecting participants are listed for 20 of 80 in the VX-150 group, 22 of 81 in the HB/APAP group, and 23 of 82 in the placebo group. These are separate from the serious adverse-event counts. The figures are descriptive and do not, by themselves, establish whether differences between arms are statistically meaningful or attributable to an intervention. No medical conclusion should be drawn from the counts alone.

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

The posted primary results show a higher average SPID24 score in the VX-150 arm than in the placebo arm. The sponsor’s ANCOVA estimated an LS mean difference of 29.50, with a 95% confidence interval from 16.61 to 42.40. The interval excludes zero, and the reported p-value is below 0.001. These statistics describe the evidence and precision for the measured group contrast under the reported analysis.

The result is specific to the trial population, endpoint definition, and assessment period: randomized participants who received at least one dose, measured using time-weighted pain-intensity differences from 0 to 24 hours after the first dose. It does not establish what the comparison would be for people outside the studied population, for other pain conditions, for other periods, or for outcomes that were not measured or posted.

The result does not show that every participant experienced the group-average difference, nor does it establish the clinical importance of the observed numerical contrast. The registry record does not report a threshold for a clinically important SPID24 difference. Statistical significance and clinical importance are different questions: a result can be estimated precisely enough to distinguish it from zero without the registry data defining how meaningful its size is.

The primary comparison is with placebo, not HB/APAP. HB/APAP was described as a standard-of-care reference arm and was not intended for statistical comparisons with VX-150. The results therefore do not establish a statistical comparison between VX-150 and HB/APAP.

The registry record also does not provide all details needed to evaluate missing-data handling, model specification, multiplicity control, or the original sample-size rationale. Those limitations qualify how fully the posted results can be independently assessed. The reported findings should be understood as evidence about the stated trial outcomes, not as a conclusion about every possible benefit or risk.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through both its estimate and its uncertainty. The primary point estimate describes the size and direction of the group contrast on a defined pain scale; its confidence interval conveys a range of values compatible with the sponsor’s analysis. The p-value alone would not provide that information.

It also highlights the distinction between adjusted and unadjusted results. The sponsor reports an ANCOVA least-squares mean difference, while a recalculation from group summaries is an unadjusted approximation. Their close point estimates offer a useful consistency check, but the model-based and summary-based intervals are not interchangeable. Readers need to know which estimate answers the trial’s stated analysis question.

The study’s three-arm design raises an important comparison issue: including a standard-of-care reference arm does not mean that every pair of arms was intended for formal inference. The registry explicitly identifies placebo as the comparator for the primary question and says HB/APAP was not intended for statistical comparisons with VX-150.

Finally, multiple secondary outcomes can add useful context while increasing the importance of a prespecified testing strategy. The registry lists a range of pain, rescue-medication, and pharmacokinetic outcomes, but does not report multiplicity procedures. Separating the primary analysis from secondary evidence helps avoid treating every favorable result as equally confirmatory. Together, endpoint definition, analysis method, precision, and reporting gaps shape a careful statistical reading of this trial.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the original sample-size justification, so the planned enrollment cannot be assessed against the trial’s intended effect size or statistical power. The sample-size illustrations based on the observed effect are not a substitute for that original rationale.

Details needed to reproduce the sponsor’s ANCOVA are not reported, including the model covariates. The registry also does not report the handling of missing primary endpoint measurements, the extent of missing data, or sensitivity analyses. These gaps limit independent evaluation of how analysis choices may have influenced the reported estimate.

The registry lists multiple secondary outcomes, but does not report a multiplicity-control strategy or testing hierarchy. Consequently, secondary findings have uncertain confirmatory status. Detailed numerical results are not reported for every listed secondary outcome in the information available for this analysis.

The primary contrast is limited to VX-150 versus placebo. HB/APAP is a reference arm that was not intended for statistical comparisons with VX-150, so its inclusion does not support an inferential claim between those two arms. The record also does not report a clinically important difference threshold for SPID24, making it difficult to relate the numerical effect to a defined level of clinical importance.

The record does not provide further participant characteristics, detailed dosing information, or the safety observation period in the information available for this analysis. Serious adverse-event counts are descriptive and should be interpreted within those reporting limits. Interim analyses and the full statistical analysis plan are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate Efficacy and Safety of VX-150 in Subjects With Acute Pain Following Bunionectomy — NCT03206749.
• Registry record last updated 2021-02-03; status last verified 2021-01.
• Results first posted 2021-02-03.
• 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.

23. Record Summary

The registry describes a completed Phase 2 randomized, double-blind, placebo-controlled, three-arm, parallel study of VX-150 for acute pain following bunionectomy. Enrollment was 243. The study started on 2017-06-29, and primary completion was recorded on 2017-12-01.

The primary endpoint was time-weighted SPID on the numeric pain rating scale from 0 to 24 hours after the first dose. The sponsor’s ANCOVA comparison of VX-150 with placebo reported an LS mean difference of 29.50 and a 95% confidence interval from 16.61 to 42.40. HB/APAP was a standard-of-care reference arm, not an intended statistical comparator for VX-150.

The registry reports zero serious adverse events and zero deaths in each arm. Important details, including the original sample-size rationale, missing-data methods, multiplicity procedures, and the full model specification, are not reported in the registry record.