Cannabinoid vs Opioid for Photorefractive Keratectomy Pain Control: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cannabinoid vs Opioid for Photorefractive Keratectomy Pain Control (NCT05477875), a randomized phase 2 study. The primary outcome is Pain as Recorded by the FACES Scale (Maximum) After First Surgery.

2. Clinical Question

3. Trial Design

This was a randomized, controlled, Phase 2 crossover study sponsored by the University of Florida. Its registry status is completed. The record lists a start date of 2024-02-01 and a primary completion date of 2025-01-22. Enrollment was 35.

The registry summary describes participants undergoing PRK in each eye sequentially. One treatment was used for one eye and the other treatment for the fellow eye two weeks later. This within-participant structure can allow comparisons that account for differences between people, because each participant receives both treatments. However, a valid analysis of such data generally needs to reflect the pairing and the order or period of treatment. The statistical plan does not report how these features were handled.

Masking is listed as none, so the study was open-label. Details about how the random allocation was generated, how treatment order was assigned, and whether allocation was concealed are not reported in the registry record. The record does not describe protocol rules for treatment adherence, rescue medication, withdrawals, or the timing of pain assessments beyond the stated primary endpoint timeframe.

The primary outcome was maximum pain on the FACES scale one week after the first surgery. The registry lists seven outcome measures and seven analyses overall. It names secondary measures that include visual acuity and patient-reported outcomes. The record does not report the original sample-size justification, the planned analysis population, or whether interim analyses were conducted. Those omissions limit how much can be inferred about the study’s original design and the intended handling of the crossover data.

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: Any patient who could not undergo surgery due to contraindications such as thin cornea, irregular astigmatism, or inability to lay flat were excluded. Patients who could not undergo sequential eye surgery due to scheduling constraints could not enroll in the study.

Preoperative

POW1

POM1

POM3

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 Pain as Recorded by the FACES Scale (Maximum) After First Surgery, measured over 1 week after first surgery.

The primary endpoint is maximum pain recorded on the Wong-Baker FACES Pain Rating Scale one week after the first PRK surgery. The registry describes the scale as a sequence of faces ranging from 0, meaning no hurt, to 10, meaning the worst pain imaginable. The posted outcome is a mean measured in units on that scale, with standard deviations describing variation among participants.

A pain rating captures a participant’s reported experience rather than a physical measurement of the eye. Recording the maximum over the assessment period focuses on the highest reported pain, which can be useful when discomfort varies over time. The registry does not specify the exact observation window used to determine the maximum or how many individual ratings contributed to it.

Using the first surgery makes the endpoint a comparison at a defined point in the treatment sequence. In a crossover study, however, the first-eye result is not itself a within-participant comparison of both treatments: the second treatment is given for the fellow eye later. The primary endpoint therefore needs to be interpreted alongside the study’s sequence and the separate analysis of the crossover data. Further details of the planned analysis are not reported in the registry record.

7. Results Posted in the Registry

• Tylenol T3: mean 1.27 versus 1.33 on control; difference -0.06 (95% CI -0.67 to 0.55), standardized effect d = -0.07; z-test p = 0.848.

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.

Uncorrected Visual Acuity of First Eye Surgery

• 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:
  • Tylenol T3: mean -0.05 versus -0.12 on control; difference 0.07 (95% CI -0.03 to 0.16), standardized effect d = 0.47; z-test p = 0.158.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tylenol T3 and the control. The interval gives the range of effects that remain compatible with the data.

Uncorrected Visual Acuity of Second Eye Surgery

• 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:
  • Tylenol T3: mean -0.07 versus -0.05 on control; difference -0.02 (95% CI -0.12 to 0.07), standardized effect d = -0.17; z-test p = 0.614.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tylenol T3 and the control. The interval gives the range of effects that remain compatible with the data.

The registry names five secondary outcomes, including uncorrected visual acuity after each surgery, patient-reported outcomes, and ocular discomfort. Numeric results are posted for visual acuity after the first and second surgeries. The other listed secondary outcomes, including PROWL-SS, the Quality of Life Refractive Correction Survey, and the Ocular Discomfort Questionnaire, do not have results reported in the registry record.

Across the two visual-acuity outcomes, the simple mean-based comparisons have confidence intervals that include zero, and the posted unadjusted p-values are 0.158 and 0.614. The registry-reported analyses for these outcomes are labelled equivalence and give p = 0.516 for each. As with the primary outcome, the equivalence margins and analysis details are not reported. These results do not provide a clear additional signal that resolves the uncertainty in the primary pain comparison.

Secondary outcomes can add context by showing whether other measured aspects of the study followed a consistent pattern. They do not replace the primary outcome, and visual acuity results address a different question from postoperative pain. In general, results across many outcomes are more likely to include chance findings when interpreted individually. If no adjustment or prespecified hierarchy is reported, unadjusted secondary p-values carry less weight than a single prespecified primary analysis.

The registry record does not report a multiplicity adjustment or a plan that establishes how secondary findings should be ranked. The secondary results are therefore best treated as exploratory context, with attention to their estimates and uncertainty rather than as independent confirmation of a treatment effect or equivalence.

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

• Uncorrected Visual Acuity of First Eye Surgery
• PROWL-SS
• Quality of Life Refractive Correction Survey
• Ocular Discomfort Questionnaire
• Uncorrected Visual Acuity of Second Eye Surgery

9. Statistical Interpretation

10. Statistical Methods Explained

The posted arm summaries describe a continuous outcome using means and standard deviations. A mean gives the average score in a group; a standard deviation describes how spread out individual scores are around that average. In general, group means can be compared by estimating their difference, while the spread and number of observations determine how precisely that difference is estimated.

The simple re-calculation compares the Tylenol T3 mean with the cannabidiol mean. The reported estimate is -0.06, with a confidence interval from -0.674 to 0.554 and p = 0.848. The direction of the estimate follows that subtraction order: a negative value means the Tylenol T3 mean was lower in the posted data. The scale description assigns lower scores to less reported pain, but this estimate alone does not establish a reliable treatment difference.

In general, a confidence interval gives a range of values compatible with the data under the assumptions of the method. It represents uncertainty around an estimate; it is not a range containing a specified proportion of individual participants’ scores. An interval that crosses zero includes both a possible negative difference and a possible positive difference. Its breadth helps show how precisely the group difference is estimated.

The re-calculation is described as a simple, unadjusted comparison based on posted summary statistics. It is not the same as an analysis that uses a participant’s results under both treatments as a paired crossover observation. Pairing can be informative because each participant serves as their own comparison, but the analysis must account for the relationship between the two observations. The reported summaries do not provide the within-person covariance or the other information needed to reconstruct a paired analysis. The registry record does not report a detailed statistical plan explaining how this feature was handled.

The sponsor-reported analysis is a Wilcoxon (Mann-Whitney) test with p = 0.538. In general, this rank-based method compares the ordering of observations across groups rather than estimating a difference between arithmetic means. It can be useful when an analysis is based on ranks, but its result does not directly answer the same question as a mean difference and its confidence interval. The registry labels the analysis as equivalence, but the equivalence margin and associated decision procedure are not reported in the registry record.

In general, an equivalence analysis asks whether the difference is sufficiently small to fall within a prespecified range considered negligible for the study’s purpose. That range must be defined in advance and interpreted with an appropriate analysis. Without the margin, the reported p-value cannot establish what range of differences was considered acceptable. The record also does not state whether the reported rank test was adjusted for treatment period or order.

The study is described as randomized and crossover, with surgery on each eye sequentially and the fellow-eye treatment given two weeks later. Such a design raises general statistical questions about within-person dependence, the period in which each treatment is received, and whether the first treatment could influence measurement during the later period. Whether these issues were assessed, and how they were addressed, is not reported in the registry record.

The simple mean-based re-calculation and the sponsor’s rank-based analysis therefore provide different summaries of the available comparison. They should not be treated as interchangeable tests. The registry-reported method is the sponsor’s stated analysis; the simple comparison provides an additional view of the posted group means and their uncertainty. Neither should be interpreted beyond the information and assumptions it contains.

Finally, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the model assumptions. In general, it is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. Interpretation should consider the estimated difference, its interval, the study design, and the questions that the registry record leaves unanswered.

11. Confidence Intervals and Precision

The unadjusted mean difference for the primary pain outcome is -0.06, with a confidence interval from -0.674 to 0.554. Because the interval spans zero, the data are compatible with no mean difference as well as with differences in either direction. The estimate is close to zero, but the interval shows that the study’s result is not precise enough to confine plausible differences to a narrow range around that estimate.

In general, interval width reflects both the variability of the outcome and the amount of information available. The reported primary groups contain 16 and 19 observations, and their standard deviations are 0.95 and 0.89. With limited observations, uncertainty can remain substantial even when the group means look similar. The posted interval is for a simple unadjusted mean comparison; it does not account for crossover pairing.

The registry’s Wilcoxon analysis does not include a confidence interval. Nor does the registry report an equivalence margin that would let readers compare an interval with a prespecified acceptable range. As a result, the reported p-value labelled as equivalence cannot be used to assess the precision of an equivalence claim.

Precision is distinct from statistical significance and from clinical importance. A narrow interval can indicate a precise estimate without establishing importance, while a wide interval can leave important differences unresolved. The primary result should therefore be read as an uncertain estimate from this study, rather than as proof of equality or proof of a difference. The registry record does not report a clinically meaningful difference threshold for this pain scale.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations report participants per arm, not total events. They use the observed effect as an input and show the planned number per arm under different fractions of that effect. For the primary outcome, the entry based on 100% of the observed effect gives 3,673 participants per arm for 80% power and 4,917 participants per arm for 90% power. Planning for 75% of the observed effect gives 6,530 participants per arm for 80% power and 8,741 participants per arm for 90% power. Planning for 50% of the observed effect gives 14,692 participants per arm for 80% power and 19,668 participants per arm for 90% power.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record; these calculations are planning illustrations based on the posted result.

In general, the 80% power column describes a planned sample size intended to give an 80% chance of detecting the specified effect under the stated assumptions if that effect is present. The 90% column uses a higher target chance of detection and therefore calls for more participants under the same assumptions. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants.

These figures are not observed power. They are not a retrospective measure of how likely the completed study was to detect an effect, and they do not establish that the trial was designed around these assumptions. Their scale should be interpreted in light of the small observed mean difference and the uncertainty in that estimate.

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 = -0.060; pooled standard deviation σ = 0.918.
2. n = 2 × (1.96 + 0.842)² × 0.918² / -0.060² = 3,672.8, rounded up to 3,673 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 <- -0.0600000000000001                      # observed difference in means
sigma <- 0.917759128628976                     # 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(5477875)
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 = 3,673 (80% power), 4,917 (90% power)
 75% of observed effect: n per arm = 6,530 (80% power), 8,741 (90% power)
 50% of observed effect: n per arm = 14,692 (80% power), 19,668 (90% power)
power.t.test: 3673.7 
Simulated power at n = 3,673 per arm: 0.806 (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 a sponsor analysis using a Wilcoxon (Mann-Whitney) method, with p = 0.538, and labels it as an equivalence analysis. The simple re-calculation instead compares the posted group means and gives a mean difference of -0.06, a confidence interval from -0.674 to 0.554, and p = 0.848. These results differ because they summarize the comparison using different statistical methods and answer different immediate questions: the rank test is not a direct test of the arithmetic mean difference.

The record does not report the equivalence margin or the detailed procedure needed to interpret the sponsor’s equivalence label. It also does not provide a confidence interval for that rank-based analysis. Therefore the sponsor-reported p-value cannot be used to determine whether a prespecified equivalence criterion was met from the registry record alone.

The posted mean-based calculation is an unadjusted re-calculation from summary statistics, not a replacement for the sponsor’s analysis. It does not use the within-participant pairing that may be available in a crossover design. The record does not give enough details to determine how the sponsor handled pairing, sequence, or period. The two analyses should be read as distinct statistical summaries, with their methods and limitations kept explicit.

15. Multiplicity, Missing Data and Analysis Populations

The record lists seven outcome measures and seven analyses, including a primary pain outcome and secondary measures. It does not report whether the analyses were arranged in a prespecified hierarchy, whether a multiplicity adjustment was planned, or whether particular outcomes were designated as confirmatory versus exploratory beyond the primary and secondary labels.

In general, testing several outcomes can increase the chance that at least one result appears unusual by chance. Multiplicity methods adjust the interpretation or thresholds to account for multiple comparisons. Without a reported plan, the unadjusted p-values for secondary outcomes should not be read as if each were the only analysis conducted. The registry does not report an adjustment, so no adjustment should be assumed.

The registry also does not describe missing-data handling, the number of participants with observed data at each assessment, or whether the primary analysis included all randomized participants. Although the posted primary groups have 16 and 19 observations, those counts alone do not explain whether other participants were excluded, had missing measurements, or were not included for another reason. Reasons for missingness and methods used to address it are not reported in the registry record.

Analysis populations are not described. The record does not state whether analyses followed an intention-to-treat principle, included only participants who received both treatments, or used another population definition. It also does not report how incomplete crossover pairs, treatment adherence, or deviations from assigned sequence were handled.

These omissions matter because missing observations and analysis choices can affect both estimates and their uncertainty. In a crossover study, the availability of data from both treatment periods can be particularly relevant to a paired comparison. Without the prespecified analysis plan and participant-level accounting, the extent of these effects cannot be assessed from the registry record.

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 0% reporting threshold.

For cannabidiol, the registry lists 35 participants at risk for serious adverse events and 0 affected; it also lists 35 at risk for other adverse events and 0 affected. For Tylenol T3, the corresponding figures are 35 at risk and 0 affected for serious adverse events, and 35 at risk and 0 affected for other adverse events. The deaths count is 0 for each treatment. No serious adverse-event terms are listed.

These are the adverse-event counts reported in the registry record. They describe what was recorded during the study, not a guarantee that no adverse events can occur. The crossover design means treatment-specific at-risk counts should not automatically be interpreted as independent sets of participants. The registry does not report further details about event collection, exposure duration, attribution, or whether all participants completed both treatment periods.

Zero recorded events in this study provides limited information about uncommon events or events outside the observation period. The registry does not give additional safety analyses or a fuller account of adverse-event monitoring, so the counts should be interpreted narrowly as the posted figures.

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

The posted primary data show similar group mean pain scores after the first surgery: 1.33 for cannabidiol and 1.27 for Tylenol T3. The unadjusted mean difference is -0.06, and its confidence interval includes zero while extending in both directions. The registry’s rank-based analysis is reported with p = 0.538 and labelled equivalence, but the information needed to interpret equivalence is not reported.

These findings do not establish that the treatments are identical, that one is better, or that a meaningful difference has been ruled out. A lack of a clear difference in the posted analysis is not the same as proof of equivalence. In particular, the registry does not provide an equivalence margin or a confidence interval for its reported equivalence analysis.

The result is specific to the primary endpoint, the first surgery, the stated one-week timeframe, and the participants represented in the posted data. It does not answer every question about pain at other times, the second surgery, other outcomes, or broader populations. The crossover design could support within-person comparisons, but the registry does not report enough analysis detail to determine how the paired structure was handled.

The findings should therefore be understood as an imprecise estimate from a completed randomized crossover study, alongside a registry-reported rank test whose equivalence criteria are not described. They are informative about the observed scores and the limits of their precision, but they do not justify a broader conclusion about treatment performance or clinical choice.

18. Why This Trial Matters Statistically

This trial is statistically notable because its crossover structure and its posted analyses raise distinct questions. When participants receive both treatments at different operations, paired data may contain information about within-person differences. A simple comparison of group means does not use that pairing, and the registry does not provide sufficient detail to determine how the sponsor’s analysis treated the design.

The distinction between a test for difference and an equivalence analysis is also important. A conventional non-significant result does not establish equivalence. An equivalence claim depends on a prespecified margin and an analysis that assesses whether the uncertainty lies within that margin. The registry labels its Wilcoxon result as equivalence but does not report the margin or an equivalence confidence interval, leaving that claim difficult to evaluate from the record.

The study also illustrates why effect estimates and confidence intervals matter alongside p-values. The mean difference is small, but its interval is broad enough to leave uncertainty about the direction and size of a population difference. The posted analysis is therefore more informative when read as an estimate with uncertainty than as a binary significant-or-not-significant verdict.

Finally, the sample-size illustrations translate the observed effect into planning scenarios, but they are not evidence about the study’s original design or its achieved power. Keeping design, analysis, precision, and planning separate helps readers understand what the registry record can support—and what it leaves unresolved.

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 gives limited detail about implementation of the crossover design. It describes sequential surgery on each eye, with the other treatment for the fellow eye two weeks later, but treatment order, sequence allocation, and any assessment of period or carryover effects are not reported. The absence of masking may also matter for a participant-reported pain score, although the record does not describe any assessment of that potential influence.

The primary posted group summaries do not show the within-participant relationship between observations. The simple mean-based re-calculation therefore does not use a paired comparison. The sponsor’s reported Wilcoxon (Mann-Whitney) analysis is not accompanied by enough information to establish how the crossover features were incorporated.

The registry does not report the original sample-size justification, the planned equivalence margin, a detailed statistical analysis plan, or the handling of missing data and analysis populations. Nor does it explain the number of participants contributing to each assessment beyond the posted group counts. These gaps limit assessment of the analysis choices and of the possible effect of incomplete observations.

The primary outcome is a maximum pain score at one stated time point. The record does not specify the exact assessment window used to define the maximum, or provide the distribution of individual scores. The secondary outcomes are also incompletely reported: numerical results are available for visual acuity after the two surgeries, while results for the other named patient-reported outcomes are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Cannabinoid vs Opioid for Photorefractive Keratectomy Pain Control — NCT05477875.
• Registry record last updated 2025-08-07; status last verified 2025-06.
• Results first posted 2025-08-07.
• 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

NCT05477875 is a completed randomized, open-label, Phase 2 crossover study sponsored by the University of Florida. It enrolled 35 participants undergoing PRK and compared oral cannabidiol with oral codeine/acetaminophen, listed in the results as Tylenol T3. The registry summary describes treatment of each eye at sequential surgeries, with the fellow-eye treatment two weeks later.

The primary endpoint was maximum Wong-Baker FACES pain score one week after the first surgery. The posted group means were 1.33 and 1.27. A simple unadjusted comparison gives a mean difference of -0.06 and a confidence interval that includes zero. The registry reports a Wilcoxon analysis labelled as equivalence, but does not report an equivalence margin or a confidence interval for that analysis.

The record also posts visual-acuity results after each surgery and lists other secondary measures without numerical results. Important details about the original sample-size rationale, missing-data handling, analysis populations, and crossover-specific analysis are not reported in the registry record.