Dose-Escalation Study of HTX-034 Following Bunionectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose-Escalation Study of HTX-034 Following Bunionectomy (NCT04398329), a randomized phase 1, phase 2 study. The primary outcome is Incidence of TEAEs in Phases 1b/2.

2. Clinical Question

3. Trial Design

This completed study was a randomized, blinded, active-controlled Phase 1b/2 trial with a parallel-group model. Its title describes triple masking; the registry record does not identify which trial roles were masked. Enrollment was 78. The record lists a start date of 2020-05-08 and primary completion date of 2021-07-15.

Phase 1b evaluated escalating doses of HTX-034 compared with bupivacaine HCl. Phase 2 was a dose-expansion phase that evaluated additional participants treated with the HTX-034 dose selected based on Phase 1b, also compared with bupivacaine HCl. The registry describes low and high HTX-034 doses in both phases. The low dose was fixed, while the high dose was individualized across a stated range. Bupivacaine HCl was the active control.

For the primary endpoint, results from the phases were combined by treatment group. The registry explains that the doses for each treatment group, surgical procedure, protocol assessments, and participating sites were the same across phases, and that the combined arms were intended to provide a larger sample size. The posted primary comparison therefore does not preserve separate phase-specific estimates.

The primary outcome was incidence of treatment-emergent adverse events in participants, assessed over 42 days. Posted secondary outcomes include pharmacokinetic measures, pain scores with activity, opioid consumption, and the proportion of participants who were opioid-free. The registry lists 11 outcome measures, but not all have posted results in the information considered for these comparisons. The trial's original sample-size justification and detailed statistical 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: The data from Phase 1b and Phase 2 for PD activity and SAEs were combined for each treatment group because the dose for bupivacaine HCI, HTX-034 low dose and HTX-034 high dose were the same, in both Phases, respectively. In addition, the surgical procedure, protocol assessments, and participating sites were the same in both Phases. Pooling across cohorts was pre-specified in the SAP and was used in analysis of the primary efficacy endpoint, as well as in the sample size calculation.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: HTX-034 Phase 1b and Phase 2 low dose and Phase 1b and Phase 2 high dose Arms/Groups and Bupivacaine HCI Arm/Group was the same dose, same surgical procedure, same protocol assessments and same sites in Phase 1b and Phase 2, so the Arms are combined given the data provides a larger sample size providing more representative assessment of the 2 doses.

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: Bupivacaine HCI was the same dose, same surgical procedure, same protocol assessments and same sites in Phase 1b and Phase 2, so the Arms are combined given the data provides a larger sample size providing more representative assessment of the 2 doses.

6. Primary Endpoint

The registry lists the primary outcome as Incidence of TEAEs in Phases 1b/2, measured over 42 days.

The primary endpoint is the incidence of treatment-emergent adverse events (TEAEs) in participants across Phases 1b/2, with a 42-day timeframe. A count of participants with an event describes how many people in each treatment group experienced at least one qualifying event; it is not a count of all individual event episodes. The posted values are 17 of 22 in the HTX-034 low-dose group, 23 of 34 in the HTX-034 high-dose group, and 11 of 17 in the bupivacaine HCl group.

Adverse-event monitoring is used to characterize safety during and after exposure to study treatments. It is distinct from the pain and opioid-related outcomes: those secondary measures describe postoperative symptoms or medication use, whereas the primary endpoint records participants with TEAEs. The endpoint name and timeframe specify what was counted and when, but the registry record does not give a fuller operational definition of which events qualified or the approach to attribution.

The registry combines the phase-specific groups for this endpoint because it reports the same dose, surgical procedure, protocol assessments, and sites across phases. Combining results increases the information available for the pooled descriptive counts, but it does not make the study groups large or establish that the phases would have had identical outcomes if presented separately. The count and comparison estimates should therefore be read as results from this combined record, with uncertainty considered alongside the observed values.

7. Results Posted in the Registry

• Phases 1b/2: HTX-034 High Dose: 67.6% (23/34) versus 77.3% (17/22) on control; risk difference -9.6 percentage points (95% CI -33.2 to 13.9), risk ratio 0.88 (0.63–1.21); unadjusted two-proportion z-test p = 0.436.
• Phases 1b/2: Bupivacaine HCl: 64.7% (11/17) versus 77.3% (17/22) on control; risk difference -12.6 percentage points (95% CI -41.2 to 16.1), risk ratio 0.84 (0.55–1.27); unadjusted two-proportion z-test p = 0.387.

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.

Mean AUC of Pain Scores With Activity

• 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 deviations.
• Result:
  • Phases 1b/2: HTX-034 High Dose: mean 561.93 versus 535.70 on control; difference 26.23 (95% CI -149.89 to 202.35), standardized effect d = 0.08; z-test p = 0.770.
  • Phases 1b/2: Bupivacaine HCl: mean 607.31 versus 535.70 on control; difference 71.61 (95% CI -128.60 to 271.82), standardized effect d = 0.23; z-test p = 0.483.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Phases 1b/2: HTX-034 High Dose 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 Phases 1b/2: Bupivacaine HCl and the control. The interval gives the range of effects that remain compatible with the data.

Opioid Consumption

• 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 deviations.
• Result:
  • Phases 1b/2: HTX-034 High Dose: mean 10.87 versus 9.89 on control; difference 0.98 (95% CI -6.76 to 8.72), standardized effect d = 0.06; z-test p = 0.804.
  • Phases 1b/2: Bupivacaine HCl: mean 8.88 versus 9.89 on control; difference -1.01 (95% CI -7.20 to 5.18), standardized effect d = -0.10; z-test p = 0.749.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Phases 1b/2: HTX-034 High Dose 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 Phases 1b/2: Bupivacaine HCl and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Subjects Who Are Opioid-free

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Phases 1b/2: HTX-034 High Dose: 35.3% (12/34) versus 36.4% (8/22) on control; risk difference -1.1 percentage points (95% CI -26.8 to 24.7), risk ratio 0.97 (0.47–1.99); unadjusted two-proportion z-test p = 0.935.
  • Phases 1b/2: Bupivacaine HCI: 23.5% (4/17) versus 36.4% (8/22) on control; risk difference -12.8 percentage points (95% CI -41.3 to 15.6), risk ratio 0.65 (0.23–1.79); unadjusted two-proportion z-test p = 0.389.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Phases 1b/2: HTX-034 High Dose 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 Phases 1b/2: Bupivacaine HCI and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes span pharmacokinetic measures, pain with activity, opioid consumption, and opioid-free status. Among the numerical results described, continuous measures are reported as group means with standard deviations, while opioid-free status is reported as participant counts. The estimates and uncertainty vary across these outcome types, but their comparison intervals do not establish clear separation between groups. The results are therefore best read as exploratory descriptions alongside the primary safety endpoint, not as independent confirmation of a treatment effect.

These outcomes address different questions from the primary TEAE count. Pain scores and opioid consumption concern postoperative pain-related measures, while opioid-free status records whether participants were opioid-free over its stated timeframe. None can be used as a replacement for the primary safety endpoint, and a pattern in one outcome does not determine the interpretation of another. The posted pain and opioid measures do not resolve the uncertainty in the primary comparison.

Multiplicity matters because examining multiple outcomes and contrasts creates more opportunities to observe a seemingly notable result by chance. The registry record lists no reported analyses for the secondary endpoints, and the posted p-values are unadjusted. Without a reported hierarchy of outcomes, adjustment approach, or prespecified interpretation plan, isolated secondary findings should carry less weight than a clearly defined primary analysis. This is especially important when the study groups are limited and the estimates have broad intervals.

The secondary results can inform what was measured and how the observed data were distributed, but the registry record does not establish that these measures were powered for definitive comparisons. The original sample-size justification and detailed analysis plan are not reported. The overall secondary-outcome pattern should therefore be considered descriptive and hypothesis-generating, with uncertainty and multiplicity kept in view rather than translated into a ranking of treatments.

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

• Cmax for HTX-034
• Tmax for HTX-034
• AUClast for HTX-034
• AUCinf for HTX-034
• t½ of HTX-034
• Mean AUC of Pain Scores With Activity
• Opioid Consumption
• Proportion of Subjects Who Are Opioid-free

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary participant-level endpoint: each participant is counted according to whether a TEAE was recorded during the 42-day timeframe. The posted group summaries give the number with an event and the number of participants in each group. For comparisons, the risk difference expresses the difference between the two observed event proportions. A negative estimate means the event proportion in the named comparison group was lower than in the low-dose reference group in these data. It does not by itself establish a true treatment effect.

What does a confidence interval add?

A confidence interval gives a range of values reasonably compatible with the data under the statistical model used for the estimate. It communicates uncertainty around the point estimate, which a single estimate or p-value cannot show. For the primary comparisons, the 95% confidence intervals include zero and extend to both negative and positive values. Thus, the posted data do not estimate the direction of a difference precisely. The interval is not a guarantee that the true value lies inside it, and it does not describe the probability that a particular treatment is better.

How should the p-values be read?

The listed p-values are unadjusted. In general, a p-value assesses how compatible the data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, nor is it a measure of the clinical importance of a difference. With small groups and broad confidence intervals, a non-small p-value can coexist with substantial uncertainty. The registry record does not report a sponsor analysis for these comparisons, so the posted recalculated comparisons should be understood as unadjusted summaries rather than as a substitute for a prespecified trial analysis.

Why are continuous outcomes handled differently?

Pain scores with activity and opioid consumption are continuous outcomes reported as means and standard deviations. A mean difference compares the group averages; its confidence interval indicates uncertainty about that average difference. The standard deviation describes variability among observations within a group, not uncertainty in the mean itself. These measures have different units and meanings from the binary TEAE endpoint, so their effect estimates should not be directly compared on the same numerical scale. The registry does not report analyses for these secondary outcomes.

Why does the comparison reference matter?

The posted comparisons use the HTX-034 low-dose group as the reference. Reading the sign of a risk difference or mean difference requires keeping that reference clear: the estimate is for the named group relative to low dose, not a comparison with an abstract no-treatment group. The study included an active control, bupivacaine HCl, but the displayed pairwise estimates do not represent every possible contrast between all treatment groups. A comparison's interpretation also depends on which phase groups were combined and on the endpoint's timeframe.

What can be inferred from the design?

Randomization supports balanced assignment in expectation, while masking can reduce some forms of bias; neither guarantees balance or removes uncertainty in a small trial. The registry describes triple masking but does not specify the masked roles. The parallel-group design means participants were assigned to a treatment group rather than being reported as receiving each treatment in sequence. Phase 1b dose escalation and Phase 2 dose expansion describe the study's stages, but the detailed allocation procedures and original statistical plan are not reported in the registry record. The registry's rationale for pooling phase-specific groups is that doses, surgery, assessments, and sites were the same.

In general, sparse data can make estimates sensitive to a small number of participants. This is one reason to read effect estimates together with their intervals and group sizes rather than relying on a nominal significance threshold. No new adjustment or analysis is implied by describing the posted results. The comparisons remain unadjusted and their interpretation is limited by the information recorded for this trial.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate an outcome or contrast. In this trial, the primary event counts come from groups of 22, 34, and 17 participants. The confidence interval for the high-dose versus low-dose risk difference is -0.332 to 0.139; for bupivacaine HCl versus low dose it is -0.412 to 0.161. Each interval includes zero and allows values on both sides of no difference. The endpoints are far enough apart to indicate substantial uncertainty about the size and direction of either contrast.

The same caution applies to secondary outcomes. The confidence intervals for the posted pain-score mean differences extend from negative to positive values, as do the intervals for opioid consumption and opioid-free comparisons. The number and scale of observations differ by endpoint, and the measurements are not interchangeable. A confidence interval around a mean difference describes uncertainty in the average contrast, while a risk-difference interval describes uncertainty in the contrast between event proportions.

Wide intervals do not prove that there is no difference; they indicate that the data are compatible with a range of possible differences. Conversely, an estimate near zero should not be interpreted as proof that the groups are equivalent. Establishing equivalence or noninferiority would require a prespecified margin and an analysis designed for that question; these details are not reported in the registry record. The intervals are therefore best read as a warning against overconfident conclusions, rather than as evidence for a particular treatment ranking.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are planning illustrations based on the observed effect, not the trial's original enrollment target or design justification. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The figures consider detecting the full observed effect and smaller fractions of that effect. The trial's own original sample-size assumptions are not reported in the registry record.

In general, power is the chance that a study will detect an effect of a specified size under the planning assumptions if that effect is present. The 80% power column gives the approximate per-arm enrollment for an 80% chance of detecting the assumed effect at the stated significance level; the 90% column uses a higher target chance and therefore generally calls for more participants. These are design targets, not findings about the chance that the observed result is true.

Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm. This relationship helps explain why some rows have much larger planning estimates than others. The figures are sensitive to the observed effect used as their starting point; with small groups, that observed estimate can itself be imprecise. They should be treated as illustrations rather than precise prescriptions for a future study.

These numbers are not observed power. Observed power calculated from an effect estimate after a study is complete does not add a useful independent measure of evidence beyond the estimate and its uncertainty. The planning figures instead show how enrollment requirements would change under stated hypothetical effects and assumptions. They do not establish what sample size this trial was designed to achieve, and they should not be confused with the actual group sizes in the posted results.

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 = 0.773; treatment proportion p₁ = 0.676; average p̄ = 0.725.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6318 = 1.2382.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6281 = 0.5286.
4. n = (1.2382 + 0.5286)² / (-0.0963)² = 336.9, rounded up to 337 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 <- 0.772727272727273                          # control proportion
p1 <- 0.676470588235294                          # 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(4398329)
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 = 337 (80% power), 451 (90% power)
 75% of observed effect: n per arm = 584 (80% power), 781 (90% power)
 50% of observed effect: n per arm = 1,275 (80% power), 1,706 (90% power)
power.prop.test: 336.9 
Simulated power at n = 337 per arm: 0.799 (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

Multiplicity arises when a study makes several comparisons or evaluates multiple outcomes. Even when each individual test uses a conventional threshold, testing many hypotheses increases the chance of at least one result appearing notable by chance. The registry lists 11 outcome measures and includes secondary outcomes covering pharmacokinetics, pain scores, opioid consumption, and opioid-free status. It does not report a multiplicity adjustment or a hierarchy that would specify how these outcomes were to be interpreted together. The secondary comparisons are listed as unadjusted, and no analyses are reported for them.

The primary endpoint is identified as incidence of TEAEs in Phases 1b/2. However, the registry record does not provide a detailed statistical analysis plan, including a stated model, any adjustment strategy, or a prespecified decision rule for the treatment comparisons. The sponsor's own analysis is not reported in the registry record. The posted effect estimates and p-values should consequently be read as unadjusted comparisons, not as an account of an unretrieved confirmatory analysis.

Missing-data handling is also not reported in the registry record. The posted group sizes give the denominators used for the displayed outcomes, but do not explain whether any observations were unavailable, how missing outcomes were treated, or whether participants were analyzed according to randomized assignment. The analysis populations, such as intention-to-treat or per-protocol populations, are not described for these comparisons. No assumptions about missing outcomes or population definitions should be inferred from the counts alone.

The trial's original sample-size justification and its planned power are not reported. The separate planning illustrations based on observed effects use stated assumptions, but they do not reconstruct the original design rationale. Together, the absence of reported multiplicity procedures, missing-data methods, analysis populations, and original design assumptions limits how confidently the posted comparisons can be interpreted as confirmatory evidence.

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 non-serious adverse event terms

The registry reports serious adverse event figures separately for the Phase 1b low-dose, Phase 1b high-dose, Phase 2 low-dose, Phase 2 high-dose, and bupivacaine HCl groups. Each group has 0 listed serious adverse events, and each group has 0 deaths. The registry lists no top serious-event terms. These phase-specific safety entries should not be mistaken for the combined primary endpoint counts, which concern participants with any treatment-emergent adverse event across Phases 1b/2.

A serious adverse event is not interchangeable with any TEAE; the measures describe different event categories. The posted TEAE endpoint counts are 17 of 22, 23 of 34, and 11 of 17 for the combined low-dose, high-dose, and bupivacaine groups, respectively. Thus, the zero serious-event figures do not mean that no adverse events occurred. They indicate only what was recorded for the serious-event measure in the registry.

These safety counts are descriptive and come from small groups. They do not establish that serious events cannot occur or that the regimens have identical safety profiles. The registry record does not give further detail on event definitions or a statistical comparison for serious adverse events.

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

The results describe a randomized, blinded, active-controlled study of escalating and expanded HTX-034 doses compared with bupivacaine HCl following bunionectomy. The primary endpoint records participants with TEAEs over 42 days. The posted counts and unadjusted comparisons show the observations in the combined phase groups and the uncertainty around their contrasts. They do not establish that one regimen is better, worse, equivalent, or noninferior to another.

Confidence intervals for the primary risk differences include zero and span both negative and positive values. This means the observed data do not identify the direction of a difference precisely. The unadjusted p-values do not change that interpretation, and a non-significant comparison is not evidence that groups are equivalent. A claim of equivalence would require a prespecified margin and suitable design and analysis, which are not reported in the registry record.

The secondary endpoints likewise provide descriptive information about pain scores, opioid use, opioid-free status, and pharmacokinetic measures. They have distinct meanings and timeframes, and the record does not report analyses for the secondary comparisons. Their results should not be treated as decisive support for the primary finding or as a basis for a treatment recommendation. The comparisons also do not describe outcomes beyond the study's participants, procedure, and recorded observation periods.

For clinical interpretation, the registry results alone do not provide all information needed to assess the complete evidence base. The record does not report detailed missing-data methods, analysis populations, multiplicity handling, the original sample-size justification, or a full statistical analysis plan. The results can be used to understand what this trial recorded and how uncertain the reported estimates are; they should not be converted into advice about treatment choice or expectations for an individual patient.

17. Why This Trial Matters Statistically

This trial is statistically informative as an example of why effect estimates need to be read with their uncertainty. The primary endpoint counts may look straightforward, but the comparisons are based on modest group sizes and have confidence intervals that include zero and allow differences in either direction. Reporting an estimate and interval makes that imprecision visible; interpreting only the direction of a point estimate or a p-value would miss it.

The trial also illustrates the distinction between an endpoint's observed count and the contrast used to compare groups. The primary endpoint is a participant count, while the posted pairwise statistics express risk differences against the low-dose reference group. Secondary outcomes use other scales, including means and mean differences. Keeping the outcome definition, denominator, reference group, and unit in view is essential to interpreting each result correctly.

Combining Phase 1b and Phase 2 results has an explicit rationale in the registry record: doses, procedure, assessments, and sites were the same across phases. This makes the pooling decision visible, while also reminding readers that the displayed primary results are combined rather than phase-specific. The record's missing details about analysis populations, missing outcomes, multiplicity, and original planning assumptions demonstrate why registry results should be accompanied by a transparent statistical plan.

Finally, planning calculations based on observed effects are not the same as evidence that a completed study had adequate power. They are illustrations under assumptions and can change substantially when the effect target changes. Separating those design illustrations from the trial's observed results helps prevent a planning figure from being mistaken for a measure of what the study actually demonstrated.

18. Limitations

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

The primary outcome combines Phase 1b and Phase 2 participants. Although the registry gives reasons for combining the phase-specific groups, pooled estimates do not show whether results differed by phase. Phase-specific primary comparisons are not reported in the presented record. The group sizes remain limited, and the primary confidence intervals are broad, leaving substantial uncertainty about the risk differences.

The registry record does not report the original sample-size justification, detailed statistical analysis plan, missing-data methods, or analysis populations. It also does not report a multiplicity procedure for the numerous outcomes and comparisons. These omissions restrict assessment of whether the posted analyses match the original prespecified plan and how missing observations or multiple testing may affect interpretation.

The posted secondary results cover different outcome types and timeframes. Their unadjusted comparisons are not reported as formal sponsor analyses, and the record gives no detailed analysis for the secondary endpoints. The primary endpoint's description does not fully specify event qualification or attribution. Serious adverse-event entries are available by phase group, but they do not replace the broader TEAE endpoint and do not provide detailed comparative safety analyses.

Generalization is also limited by the study context: participants underwent unilateral first metatarsal bunionectomy with osteotomy and internal fixation, and the outcomes concern specified postoperative periods. The registry record does not support conclusions about other procedures, populations, or longer-term outcomes. These limitations counsel against treating the descriptive estimates as definitive evidence or as a basis for choosing treatment.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Dose-Escalation Study of HTX-034 Following Bunionectomy — NCT04398329.
• Registry record last updated 2026-06-09; status last verified 2026-06.
• Results first posted 2026-06-09.
• 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

NCT04398329 is a completed randomized, blinded, active-controlled Phase 1b/2 parallel-group study of HTX-034 after bunionectomy. It enrolled 78 participants and compared low- and high-dose HTX-034 with bupivacaine HCl. Phase 1b evaluated escalating doses; Phase 2 expanded evaluation of a dose selected based on Phase 1b.

The primary endpoint was incidence of TEAEs over 42 days, with phase results combined by treatment group. The posted unadjusted risk-difference intervals include zero and are broad. Secondary results cover pain scores, opioid consumption, opioid-free status, and other listed outcomes, but the record does not report analyses for the secondary comparisons. Original sample-size assumptions, multiplicity handling, missing-data methods, and analysis populations are not reported in the registry record.