A Study to Characterize the Abuse Liability of ALO-02 in Healthy, Non-Dependent, Recreational Opioid Users When ALO-02 Capsules Are Crushed and Snorted: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Characterize the Abuse Liability of ALO-02 in Healthy, Non-Dependent, Recreational Opioid Users When ALO-02 Capsules Are Crushed and Snorted (NCT01775189), a randomized phase 1 study. The primary outcome is Drug Liking: Peak Effect (Emax).

2. Clinical Question

3. Trial Design

The registry describes a completed phase 1, randomized, double-blind, placebo-controlled, single-dose, four-way crossover study. Its stated purpose was to characterize the relative abuse potential of ALO-02 when crushed and administered intranasally, in comparison with oxycodone immediate release and placebo, among non-dependent recreational opioid users. The study title and brief summary also identify crushing and snorting as the administration context of interest.

A crossover design means that participants contribute measurements under more than one treatment condition, rather than being assigned to only one condition for the entire study. The primary endpoint population was defined by completion of all 4 treatment periods and by contribution of post-dose pharmacodynamic data in each period. That definition matters when interpreting the reported group summaries: although enrollment was 45, the primary endpoint summaries report 28 participants for each of the four treatment conditions. The registry record does not report the treatment sequences or the details of the period and carryover assumptions used in the analysis.

The four conditions represented active ALO-02, active oxycodone immediate release, and two distinct placebo formulations. The primary outcome was Drug Liking: Peak Effect (Emax), measured over the intervention period at post-dose assessment times extending from 0.25 to 24 hours. The registry reports a completer analysis set for this outcome. It also lists secondary measures related to taking the drug again, overall drug liking, and any drug effects.

Enrollment was 45, and the study status is completed. The registry record does not report the original sample-size justification or the detailed statistical analysis plan. Consequently, the posted results can describe the analyzed participants and observed comparisons, but cannot establish the assumptions that informed the original trial’s design.

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: After successful naloxone challenge test, all participants underwent training sessions involving complete pharmacodynamics test battery before the drug discrimination phase, to ensure that participants fully understood how to perform the tests, were comfortable, and attained a stable level of performance on the various performance-based measures.

Only the first 6 of 7 groups are shown.

Naloxone Challenge Phase

Drug Discrimination Phase: Day 1

Reasons for not completing this period:

Drug Discrimination Phase: Day 2

Reasons for not completing this period:

Treatment Phase: First Intervention

Analysis population for the primary outcome, as defined in the registry: Completer analysis set included all randomized participants who completed all 4 periods of treatment phase and who contributed to post-dose Pharmacodynamic (PD) data from each period.

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: Safety analysis set included all participants who received at least 1 dose of study drug, beginning with the naloxone challenge phase.

6. Primary Endpoint

The registry lists the primary outcome as Drug Liking: Peak Effect (Emax), measured over Intervention period: 0.25, 0.5, 0.75, 1, 1.5, 2, 2.5, 3, 4, 6, 8, 12, 24 hours post-dose.

The primary endpoint, Drug Liking: Peak Effect (Emax), measures the highest observed response to the question about how much a participant likes the drug effect at that moment. The registry describes a 100 millimeter bipolar visual analogue scale: 0 mm represents strong disliking, 50 mm is the neutral anchor of neither like nor dislike, and 100 mm represents strong liking. Emax is the maximum observed score across the specified post-dose assessment times, from 0.25 to 24 hours.

This endpoint captures a participant’s subjective appraisal of a drug effect. In an abuse-liability study, such ratings are relevant because liking is one aspect of the experience being evaluated, and the registry’s stated purpose focuses on the potential for abuse after crushing and intranasal administration. The measure does not directly record whether someone would later use a drug, nor does a score alone establish a clinical outcome. It should be interpreted as a structured, self-reported response within the study conditions and population.

The primary analysis population was the completer analysis set: randomized participants who completed all 4 periods and contributed post-dose pharmacodynamic data from every period. The registry reports means and standard deviations for this endpoint. The posted means were 50.9 mm for placebo sugar spheres, 60.5 mm for ALO-02 30 mg, 51.3 mm for placebo lactose tablet, and 92.8 mm for oxycodone 30 mg, with 28 participants represented in each condition. The scale’s neutral anchor helps describe the location of these means, while the comparison estimates and their uncertainty address differences between conditions.

7. Results Posted in the Registry

• ALO-02 30 mg: mean 60.50 versus 50.90 on control; difference 9.60 (95% CI 5.12 to 14.08), standardized effect d = 1.12; z-test p = <0.001.
• Placebo Lactose Tablet: mean 51.30 versus 50.90 on control; difference 0.40 (95% CI -0.91 to 1.71), standardized effect d = 0.16; z-test p = 0.548.
• Oxycodone 30 mg: mean 92.80 versus 50.90 on control; difference 41.90 (95% CI 37.44 to 46.36), standardized effect d = 4.92; 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.

Take Drug Again: Peak Effect (Emax)

• 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:
  • ALO-02 30 mg: mean 58.30 versus 48.00 on control; difference 10.30 (95% CI -2.77 to 23.37), standardized effect d = 0.41; z-test p = 0.123.
  • Placebo Lactose Tablet: mean 46.60 versus 48.00 on control; difference -1.40 (95% CI -10.27 to 7.47), standardized effect d = -0.08; z-test p = 0.757.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ALO-02 30 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo Lactose Tablet and the control. The interval gives the range of effects that remain compatible with the data.

Take Drug Again: Mean Effect (Emean)

• 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:
  • ALO-02 30 mg: mean 52.16 versus 44.71 on control; difference 7.45 (95% CI -5.17 to 20.07), standardized effect d = 0.31; z-test p = 0.247.
  • Placebo Lactose Tablet: mean 43.95 versus 44.71 on control; difference -0.76 (95% CI -9.20 to 7.68), standardized effect d = -0.05; z-test p = 0.860.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ALO-02 30 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo Lactose Tablet and the control. The interval gives the range of effects that remain compatible with the data.

Overall Drug Liking: Peak Effect (Emax)

• 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:
  • ALO-02 30 mg: mean 59.90 versus 50.50 on control; difference 9.40 (95% CI 1.36 to 17.44), standardized effect d = 0.61; z-test p = 0.022.
  • Placebo Lactose Tablet: mean 51.50 versus 50.50 on control; difference 1.00 (95% CI -1.46 to 3.46), standardized effect d = 0.21; z-test p = 0.426.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for ALO-02 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Placebo Lactose Tablet and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary measures covering taking the drug again, overall drug liking, and any drug effects, including peak and mean ratings and effects over specified post-dose intervals. The posted secondary summaries give a mixed pattern rather than a single uniform signal across measures. In the summaries available for interpretation, some ALO-02 contrasts with placebo have estimates above zero and intervals that exclude zero, while the take-drug-again contrasts have intervals that include zero. This indicates that the degree of statistical support differs across outcome domains.

The secondary outcomes are related to the primary endpoint because they assess other aspects of participants’ subjective responses. They are not interchangeable with peak drug liking: an assessment of whether participants would take a drug again, an average rating over time, and a measure of any drug effect address different questions. The pattern across outcomes can add context to the primary finding, but it does not replace the primary endpoint or establish a broad conclusion about abuse liability.

Secondary comparisons generally warrant more caution when many outcomes and contrasts are examined. Each additional test creates another opportunity for a result to appear notable by chance, particularly when no adjustment is made. Whether multiplicity adjustments were applied to these outcomes is not reported in the registry record. The registry record also lists 31 posted secondary outcome results, while the study includes multiple measures and analysis comparisons. The number of results makes it especially important not to treat an isolated secondary p-value as definitive evidence.

The secondary summaries include unadjusted recalculations, and no sponsor-reported analyses are listed for the specific secondary outcomes included in those summaries. Their estimates and intervals should therefore be understood as descriptive, unadjusted contrasts from the posted summary statistics. The broader pattern is informative as context, but the secondary findings carry less inferential weight than the sponsor’s reported primary analysis.

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

• Take Drug Again: Peak Effect (Emax)
• Take Drug Again: Mean Effect (Emean)
• Take Drug Again Effect at Hours 12 and 24
• Overall Drug Liking: Peak Effect (Emax)
• Overall Drug Liking: Mean Effect (Emean)
• Overall Drug Liking Effect at Hours 12 and 24
• Any Drug Effects: Peak Effect (Emax)
• Any Drug Effects: Area Under Effect Curve (AUE) From 0-1 Hour, 0-2 Hour, 0-8 Hour and 0-24 Hour

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score measured in millimeters rather than a category such as yes or no. The registry reports group means and standard deviations. A mean describes the central level of the observed scores, while a standard deviation describes how spread out scores were around the mean. These summaries are useful for describing each condition, but they do not by themselves incorporate all features of a crossover analysis.

What does a mean difference describe?

A mean difference expresses the estimated separation between two condition means on the original endpoint scale. For the primary endpoint, the units are millimeters on the drug-liking visual analogue scale. A positive or negative sign depends on the order in which the conditions are contrasted. The registry’s reported results use least-squares mean differences from mixed models; the separate recalculations are unadjusted comparisons based on the posted summary statistics. These estimates can be close without being identical because they arise from different methods and inputs.

In a crossover study, each participant can contribute information under several conditions. A mixed model can represent the study’s repeated observations and account for features of the design included in that model. The registry identifies the sponsor’s method as Mixed Models Analysis. However, the model specification, covariance structure, treatment-sequence terms, period terms, and other details are not reported in the registry record. No further description of those model choices can be inferred from the method label alone.

How should a confidence interval be read?

A confidence interval gives a range of estimates compatible with the data and the analysis assumptions at the stated confidence level. A narrower interval indicates greater precision for that estimate; a wider interval indicates less precision. For the sponsor’s ALO-02 versus placebo sugar spheres comparison, the 95% interval runs from 4.8 to 14.2 mm around the reported least-squares mean difference of 9.5 mm. This conveys both the estimated direction and the range of uncertainty under the reported model. It is not a guarantee that the true value lies inside the interval.

The recalculated intervals are based on posted summary statistics and are not substitutes for the sponsor’s model-based intervals. Since the study is a crossover, the relationship between a participant’s measurements across conditions can matter for precision. The summary-statistic recalculation does not reproduce every aspect of a participant-level mixed model. The registry record flags a discrepancy, so the sponsor’s own analysis should be used as the main inferential result.

What does a p-value add?

A p-value describes how unusual data at least as incompatible with a null comparison would be under the assumptions of the specified analysis, if the null comparison were true. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of a difference. For the primary ALO-02 versus placebo comparison, the sponsor reports p < 0.001. That result should be considered together with the estimated difference, confidence interval, endpoint scale, analysis population, and the number of outcomes and contrasts under consideration.

The registry’s reported primary comparisons include multiple pairwise contrasts among the active and placebo conditions. Whether the p-values were adjusted for those comparisons is not reported in the registry record. A result that meets a conventional significance threshold in an unadjusted analysis may require more cautious interpretation when many comparisons are made. The endpoint and its inferential result remain specific to the stated contrast and analysis.

Why are the group summaries not the whole analysis?

The reported primary means are descriptive summaries for the completer analysis set. The sponsor’s mixed-model least-squares means and differences are model-based estimates. They can account for aspects of the repeated-measures design as specified in the analysis, while simple recalculations from marginal means and standard deviations cannot recover unreported participant-level relationships. This distinction is particularly relevant in a crossover study, where observations from the same participant are not independent in the way that observations from different participants may be.

The primary endpoint is defined as the maximum observed rating over scheduled post-dose assessments. A maximum is an interpretable peak-response measure, but it depends on the observed assessment schedule and on which measurements are available. The registry states that the completer set had post-dose pharmacodynamic data from each period. The detailed handling of missing individual assessments and the exact derivation rules beyond the Emax definition are not reported in the registry record.

All interpretation is conditional on the study population, treatment conditions, measurement method, and analysis population. General statistical concepts help explain how estimates and uncertainty work, but do not fill gaps in the registry’s account of the original design assumptions or analysis procedures.

11. Confidence Intervals and Precision

The sponsor’s primary ALO-02 versus placebo sugar spheres estimate is a 9.5 mm least-squares mean difference. Its 95% confidence interval extends from 4.8 to 14.2 mm. The interval is entirely above zero, and the reported p-value is < 0.001. These results indicate that, under the sponsor’s mixed-model analysis, the estimated difference is positive and the interval excludes zero. The interval also makes clear that the point estimate is not known without uncertainty: a range of values remains compatible with the analysis.

The unadjusted recalculation from the posted summaries estimates a 9.6 mm mean difference, with an interval from 5.115 to 14.08. This is close to the sponsor’s reported estimate, but the recalculation is not the same as the mixed-model analysis. Because the record flags a discrepancy, the sponsor’s analysis takes precedence. The recalculated interval should be read as a simple unadjusted illustration, not as a replacement for the model-based result.

For the sponsor-reported contrast between ALO-02 and oxycodone 30 mg, the least-squares mean difference is -32.3 mm, and its 95% confidence interval extends from -37.0 to -27.6. For the placebo sugar spheres versus placebo lactose tablet contrast, the estimate is -0.4 mm, with a 95% confidence interval from -5.0 to 4.3. These intervals describe uncertainty for distinct contrasts and should not be conflated with the ALO-02 versus placebo interval.

Precision is also shaped by the analyzed population. The primary summaries include 28 participants in each condition, drawn from the completer analysis set, while enrollment was 45. The registry record does not report a confidence interval for each group mean, and it does not provide the participant-level data needed to independently reproduce the mixed model. Statistical precision in these posted contrasts should not be taken to mean that the result applies equally to people outside the study population or to other use conditions.

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 sample-size figures are planning illustrations based on observed effects, not the original trial’s sample-size rationale. For these continuous outcomes, each figure is the number of participants per arm, not a total across arms and not a count of events. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The original trial’s design assumptions are not reported in the registry record.

The 80% power column describes an illustrative design that would have an 80% probability of detecting the specified effect under the calculation assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target probability of detecting that same specified effect. These are prospective planning quantities; they do not describe the probability that the completed trial found a true effect.

Rows that plan for 100% of the observed effect use the full observed estimate as the target. Rows planning for 75% or 50% use smaller target effects. Smaller effects require more participants for a given power target, which is why the figures increase as the assumed effect becomes a smaller fraction of the observed one. The illustrations can therefore help show how strongly sample-size needs depend on the effect chosen for planning.

These figures are not observed power. They are not evidence that the completed study was designed around the observed result, and they do not replace the sponsor’s reported analysis. The registry record does not report the original sample-size justification, so the planning illustrations should be used only to understand the stated calculation assumptions and the relationship between target effect and sample size.

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 = 9.600; pooled standard deviation σ = 8.561.
2. n = 2 × (1.96 + 0.842)² × 8.561² / 9.600² = 12.5, rounded up to 13 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 <- 9.6                      # observed difference in means
sigma <- 8.56139299413361                     # 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(1775189)
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 = 13 (80% power), 17 (90% power)
 75% of observed effect: n per arm = 23 (80% power), 30 (90% power)
 50% of observed effect: n per arm = 50 (80% power), 67 (90% power)
power.t.test: 13.5 
Simulated power at n = 13 per arm: 0.782 (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 registry reports the sponsor’s primary analysis as a mixed-model comparison of least-squares means. For ALO-02 30 mg versus placebo sugar spheres, that analysis estimates a difference of 9.5 mm, with a 95% confidence interval from 4.8 to 14.2 and p < 0.001. It also reports model-based contrasts involving oxycodone and the second placebo condition. These are the sponsor’s own analyses of the study outcome.

The unadjusted recalculation using the posted arm summaries estimates an ALO-02 versus placebo sugar spheres mean difference of 9.6 mm, with an interval from 5.115 to 14.08 and p < 0.001. The recalculation is a simple comparison from summary statistics; it does not reproduce all features of the mixed-model analysis in this crossover study. The registry record marks a discrepancy between the sponsor’s analysis and the recalculation. Under that circumstance, the sponsor’s own analysis takes precedence for interpretation.

The closeness of these two estimates does not make their methods interchangeable. The sponsor’s reported least-squares means come from the stated mixed-model approach, while the recalculation is unadjusted. The registry record does not provide enough model detail or participant-level data to resolve the source of the difference independently. The most appropriate reading is therefore to use the sponsor-reported estimate, interval, and p-value as the primary inferential result, while treating the recalculation as a supplementary summary-statistic check.

The sponsor’s reported comparisons are not a complete account of all possible analysis decisions. Details such as multiplicity adjustment, model specification, and missing-data procedures are not reported in the registry record. Those omissions limit how fully the model can be assessed from the registry results alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies multiple treatment conditions, multiple pairwise comparisons, and a range of primary and secondary outcomes. When many statistical tests are conducted, the chance of at least one apparently notable result can increase. Procedures such as adjusting significance thresholds or controlling an error rate can address that issue, but whether the sponsor applied any multiplicity adjustment is not reported in the registry record. The reported p-values should therefore be interpreted as presented, without assuming a correction that is not described.

The primary analysis population is described as randomized participants who completed all 4 treatment periods and contributed post-dose pharmacodynamic data from each period. This provides a clear definition for the posted primary endpoint summaries, but it does not explain why other randomized participants were not in that set or whether the completer definition was specified before analysis. Reasons for missing endpoint data and the handling of missing observations beyond this population definition are not reported in the registry record.

The record identifies a mixed-model analysis for the sponsor’s primary comparisons, but does not report the model’s detailed specification. The registry record does not report the covariance structure, treatment-sequence or period terms, the assumptions made about missing data, or sensitivity analyses addressing those assumptions. These details matter because a crossover analysis relies on information collected within participants across treatment periods.

The record also does not report the original sample-size justification, interim analyses, or the complete statistical analysis plan. These omissions do not negate the posted results, but they limit independent assessment of prespecification, multiplicity, missing-data handling, and the full set of analyses undertaken. A cautious interpretation distinguishes what is explicitly reported—the primary population definition and mixed-model method—from procedures that remain undocumented in the registry record.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry’s serious adverse event summaries report zero participants affected in every listed group. The at-risk counts vary across groups: Naloxone has 45 at risk, oxycodone HCl 30 mg has 45, placebo oxycodone HCl has 42, placebo sugar spheres has 29, ALO-02 30 mg has 30, placebo lactose tablet has 30, and oxycodone 30 mg has 32. These figures should be read as the registry’s group-level serious adverse event counts, with the corresponding group denominators, not as a single comparison across equivalent exposure groups.

The record does not list serious adverse event terms in the top serious terms field. Deaths are not reported in the registry record. The summaries also list other adverse event counts, but a count of participants with an event does not establish that a treatment caused it. The differing at-risk counts and the study’s single-dose crossover conditions are important context when reading these safety figures.

Zero reported serious adverse events in the listed groups is a description of the registry entries, not proof that serious events cannot occur or a complete characterization of safety. The trial’s stated focus is abuse liability, and the safety summaries should be interpreted separately from the subjective drug-liking endpoint.

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

The posted primary results describe peak subjective drug-liking ratings under the study’s specific conditions: crushed products administered intranasally to healthy, non-dependent recreational opioid users in a single-dose, four-way crossover study. The sponsor’s mixed-model analysis estimates higher peak drug liking for ALO-02 than for placebo sugar spheres, and lower peak drug liking for ALO-02 than for oxycodone 30 mg. These are results for a defined endpoint and analyzed population, not a direct measure of every aspect of abuse liability.

Drug liking is a subjective rating on a bipolar scale. It captures participants’ reported experience at the time of assessment, with the peak endpoint taking the maximum observed score across scheduled times. Such a rating can inform an evaluation of abuse-related subjective effects, but it does not establish whether a participant would subsequently seek, misuse, or become dependent on a drug. Nor does the result by itself establish outcomes in patients, people with opioid dependence, or other populations not described as the study population.

The reported comparisons do not establish effects for doses, formulations, or administration routes beyond those studied. The registry’s stated conditions concern crushed ALO-02 and crushed oxycodone immediate release administered intranasally, with placebo conditions. Results should not be generalized to other use patterns from these data alone.

The sponsor’s result is a model-based analysis, while the supplementary recalculation is unadjusted. The registry record flags a discrepancy, so the sponsor’s own analysis takes precedence. The record does not report the original sample-size rationale, detailed model specification, multiplicity procedures, or full missing-data methods. These uncertainties affect how completely the analysis can be evaluated, without changing what the registry reports.

Overall, the posted data support a precise description of the measured ratings and sponsor-reported contrasts in the completer analysis set. They should not be interpreted as medical advice or as a standalone conclusion about clinical safety, real-world misuse, or treatment effects.

18. Why This Trial Matters Statistically

This trial illustrates several statistical issues that matter in clinical research. First, the endpoint is a continuous subjective rating, and its interpretation depends on the scale anchors and the timing of measurement. A peak score summarizes the maximum observed response, while other outcomes in the registry assess mean response, willingness to take the drug again, and other drug effects. Clear endpoint definitions are essential because different summaries of a participant’s experience answer different questions.

Second, the crossover design makes the structure of the data important. Participants contribute observations under multiple conditions, so analysis methods need to reflect repeated measurements within a participant. The registry identifies a mixed-model approach for the sponsor’s primary comparisons, while a simple recalculation from arm summaries is necessarily less complete. The flagged discrepancy reinforces the need to distinguish a model-based sponsor analysis from an unadjusted summary-statistic calculation.

Third, effect estimates are more informative when paired with confidence intervals. The primary sponsor-reported interval conveys the uncertainty around the estimated contrast, rather than leaving interpretation to a p-value alone. Comparisons with both an active drug and two placebos also show why comparator choice matters: each contrast addresses a different question.

Finally, the trial highlights the importance of the analysis population, multiplicity, and transparency about methods. Enrollment was 45, while the primary endpoint summaries use 28 participants per condition in the completer analysis set. The record does not report the original sample-size rationale or whether multiplicity was addressed. Recognizing these limits helps readers describe the evidence accurately without extending the result beyond the population, outcome, and conditions actually studied.

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 primary analysis is restricted to participants who completed all 4 treatment periods and contributed post-dose pharmacodynamic data from each period. The primary summaries include 28 participants per condition, compared with enrollment of 45. The registry record does not report the reasons for the difference between enrollment and the completer analysis set, or the detailed handling of missing observations. This limits assessment of how selection into the analysis population may affect interpretation.

The registry identifies a mixed-model analysis but does not report its full specification. In a crossover study, details about period effects, treatment sequence, within-participant correlation, and carryover handling can be relevant; those details are not reported in the registry record. The summary-statistic recalculations do not reproduce a participant-level model, and the record flags a discrepancy. The sponsor’s analysis therefore takes precedence, but the available record does not permit independent evaluation of all model choices.

The statistical plan’s approach to multiple outcomes and pairwise comparisons is not reported. The registry lists numerous secondary measures and comparisons, so the absence of documented multiplicity procedures makes isolated secondary findings less conclusive. The original sample-size justification and interim analyses are also not reported in the registry record.

The study population and administration context are specific: healthy, non-dependent recreational opioid users and single-dose intranasal administration of crushed products. The registry results do not establish effects in other populations, for other routes, or under other dosing conditions. Drug liking is a self-reported subjective outcome and does not directly measure later drug-taking behavior or clinical consequences. The safety summaries are group counts and do not, by themselves, establish causation or characterize risks beyond the recorded events.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Characterize the Abuse Liability of ALO-02 in Healthy, Non-Dependent, Recreational Opioid Users When ALO-02 Capsules Are Crushed and Snorted — NCT01775189.
• Registry record last updated 2017-07-17; status last verified 2017-02.
• Results first posted 2017-07-17.
• 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

NCT01775189 is a completed phase 1 randomized, double-blind, placebo-controlled, single-dose, four-way crossover study in healthy, non-dependent recreational opioid users. Enrollment was 45. The primary endpoint was peak drug liking on a 100 mm bipolar visual analogue scale, analyzed in a completer population that required completion of all 4 periods and post-dose pharmacodynamic data from each period.

The sponsor’s mixed-model analysis reported an ALO-02 versus placebo sugar spheres least-squares mean difference of 9.5 mm, with a 95% confidence interval from 4.8 to 14.2 and p < 0.001. The record flags a discrepancy with an unadjusted recalculation, so the sponsor’s analysis takes precedence. Details of the original sample-size justification, multiplicity procedures, full model specification, and missing-data methods are not reported in the registry record.