Patient Preference Comparison of AZARGA Versus COSOPT: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Patient Preference Comparison of AZARGA Versus COSOPT (NCT01340014), a randomized phase 4 study. The primary outcome is Preferred Treatment.

2. Clinical Question

This is a question about reported preference after exposure to both treatments in a particular sequence. It is distinct from asking which medication produces a better clinical outcome, and the primary endpoint does not quantify the size of a comfort difference on a continuous scale. The trial also reported ocular discomfort as a secondary outcome, measured on Day 7 of each period. The registry record does not describe the score range or its direction, so interpretation of the numerical scale should remain limited to the reported values and comparison.

3. Trial Design

The study was a Phase 4, randomized, single-masked crossover trial. Its stated purpose was to assess patient preference regarding ocular comfort after one week of instillation of each medication. In a crossover design, participants receive more than one treatment in sequence, so each participant can contribute experience with both treatments. This differs from a parallel-group design in which each participant is assigned to just one treatment. The registry record does not identify who was masked.

Participants were assigned to one of two sequences: AZARGA followed by COSOPT, or COSOPT followed by AZARGA. Each treatment period lasted 7 days, with one drop in each eye twice a day. A 48-hour washout period separated the periods. Random assignment of treatment sequence can help balance the order in which treatments are experienced, although the registry record does not report the sequence allocation counts or details of how randomization was implemented.

The registry record lists enrollment of 112 and status as completed. The primary outcome population was narrower: participants had to complete both periods and the preference questionnaire, and results were described as treated. The registry record reports 108 participants for each treatment in the primary result. It does not report the reasons participants may have been absent from the primary outcome population, nor does it describe how missing observations were handled.

Study start was recorded as 2011-09, and primary completion as 2012-10. Alcon Research is listed as the sponsor. The registry record does not report the original sample-size justification, detailed allocation ratio, planned analysis model, or specific masking procedures. The available description therefore supports an account of the treatment sequence and outcome timing, but not a reconstruction of all operational or statistical decisions.

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: This reporting group includes all enrolled participants as treated.

Period 1, First 7 Days

Reasons for not completing this period:

Period 2, Second 7 Days

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: This reporting group includes all participants who completed both treatment periods and completed the preference questionnaire, as treated.

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: This reporting group includes all participants who completed both treatment periods and completed the preference questionnaire, per planned treatment sequence (ITT full analysis population).

6. Primary Endpoint

The registry lists the primary outcome as Preferred Treatment, measured over At the end of both periods, Day 15.

The primary endpoint, Preferred Treatment, is the percentage of participants who selected AZARGA or COSOPT in response to a single question about the comfort of the two medications they had taken. The questionnaire was completed at the Day 15 visit, after both treatment periods. The reported population consists of people who completed both periods and the questionnaire, analyzed as treated.

A preference question is useful when the outcome of interest is the participant’s overall choice after direct experience with both options. In a crossover study, each participant encounters both medications, making a direct personal comparison possible. The resulting percentages describe the distribution of stated choices in the observed questionnaire population. They do not measure how large a comfort difference each participant experienced, and they do not by themselves identify which part of the experience shaped the choice.

The primary outcome is reported as 60.2% preferring AZARGA and 39.8% preferring COSOPT, with 108 participants reported for each treatment. The comparison gives a risk difference of -0.204 for COSOPT relative to AZARGA. The endpoint is therefore a categorical preference outcome, not a time-to-event measure or a continuous score. It should be read as a reported choice after both treatment periods, not as evidence about other clinical outcomes. The registry record does not report a separate validation description for the preference question or further detail on how responses were collected beyond the single-question description.

7. Results Posted in the Registry

• COSOPT: 39.8% (43/108) versus 60.2% (65/108) on control; risk difference -20.4 percentage points (95% CI -33.4 to -7.3), risk ratio 0.66 (0.50–0.87); unadjusted two-proportion z-test p = 0.003.

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.

Ocular Discomfort

• 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:
  • COSOPT: mean 3.70 versus 2.60 on control; difference 1.10 (95% CI 0.44 to 1.76), standardized effect d = 0.45; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for COSOPT than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcome provides another perspective on the study’s focus on comfort: it records ocular-discomfort scores at Day 7 of each treatment period, while the primary outcome asks participants to choose a preferred medication after experiencing both. The posted secondary comparison and the primary preference result point in a broadly similar direction in the sense that the treatment with the higher reported discomfort mean was less often selected as the preferred treatment. This is a descriptive alignment between two different measures, not proof that the score caused the preference.

The outcomes are related in subject matter but are not interchangeable. A single choice after both periods captures an overall judgment, whereas a score recorded during each period captures a numerical response at a specified time. They may reflect different aspects of experience and have different measurement properties. In particular, the registry record does not report the discomfort scale’s range or direction, its interpretation anchors, or how missing score observations were handled.

The posted secondary result has an unadjusted p-value. General explanation: when several outcomes or comparisons are examined, the chance of obtaining at least one small p-value can increase if no multiplicity strategy is used. The registry record lists one secondary outcome and two outcome measures, but does not describe a testing hierarchy, adjustment, or whether the secondary analysis was confirmatory. Therefore, the secondary result is useful as supporting context but should carry less weight than a result arising from a clearly prespecified and fully described testing plan.

The record does not report a set of secondary analyses beyond the posted ocular-discomfort result. It also does not provide a complete analysis plan or a clear account of how the repeated observations from the crossover periods were handled. These omissions constrain interpretation of the relationship between the outcomes. The pattern can be noted, but it should not be treated as independent confirmation without considering shared participants, related outcome content, and the unreported analysis details.

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

• Ocular Discomfort

9. Statistical Interpretation

10. Statistical Methods Explained

The posted results include a binary primary outcome and a continuous secondary outcome. General statistical explanations help clarify what their estimates communicate, but the registry record does not give a full analysis plan or model description. In particular, it does not state whether the reported analyses accounted for the fact that participants received both treatments.

What does a percentage preference measure?

The primary endpoint divides responses into a choice for AZARGA or a choice for COSOPT and reports each as a percentage of participants. In general, a percentage describes the share of the analyzed group in a category; it does not show how strongly participants felt or how much comfort differed for each person. The registry record reports 60.2% for AZARGA and 39.8% for COSOPT, with 108 participants reported for each treatment. These are outcome summaries, not separate treatment groups in the ordinary parallel-group sense: the trial schedule says participants received both medications.

The comparison gives a risk difference for COSOPT relative to AZARGA. In general, a risk difference subtracts one event proportion from another, using the comparison’s specified order. Here, the posted estimate is -0.204, and the confidence interval ranges from -0.334 to -0.073. The sign and order are important: a negative estimate indicates a smaller proportion for COSOPT than for AZARGA in this comparison. The registry record also posts relative measures, but the risk difference expresses the contrast in absolute proportion units and is often more directly interpretable for the observed group.

What does the p-value say?

The unadjusted p-value for the primary comparison is 0.003. General explanation: a p-value describes how incompatible the observed data, or data more extreme, would be with a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of the difference. The registry record does not state the exact model or test behind the posted p-value, so it should be described as the reported unadjusted value rather than attributed to a particular test.

“Unadjusted” also matters because the record does not report a correction for considering multiple outcomes or analyses. A p-value should not be interpreted in isolation from the study design, endpoint definition, analysis population, and precision of the estimate. The record lists no reported analyses, so details needed to reproduce or fully evaluate the analysis are not reported in the registry record.

How should the continuous outcome be read?

Ocular discomfort is reported as a mean and standard deviation for each treatment at Day 7 of each period. The mean is the group’s average score. The standard deviation describes how spread out scores were around that average; it is not the uncertainty in the estimated mean. The posted mean is 2.6 for AZARGA, with a standard deviation of 2.27, and 3.7 for COSOPT, with a standard deviation of 2.63. The reported mean difference for COSOPT relative to AZARGA is 1.1, with a confidence interval from 0.445 to 1.755 and an unadjusted p-value of 0.001.

General explanation: a mean difference summarizes the contrast in average scores, while its confidence interval conveys uncertainty around that contrast. The registry record does not report the scale’s possible range, anchors, or direction. Consequently, it is not appropriate to infer a score interpretation beyond the outcome label and numerical comparison. The record also does not identify whether the analysis used a paired method appropriate to repeated measurements or an alternative approach.

Why does the crossover structure matter?

General explanation: crossover data contain within-participant observations, which are usually related because the same person experiences more than one treatment. Analyses may need to account for that pairing, along with period and sequence. The relationship between paired observations can affect the uncertainty of a treatment contrast. The posted record gives treatment summaries and comparisons but does not report the model, covariance assumptions, sequence effects, period effects, or carryover assessment. Those details cannot be inferred from the fact that the study was randomized and crossover.

The sequence descriptions show that participants received one treatment first and the other afterward, separated by a 48-hour washout. Randomization concerns assignment to the sequence; it does not by itself guarantee that all features of a crossover analysis have been addressed. The registry record does not explain whether the primary preference outcome was analyzed as a paired comparison, how period order was considered, or whether any participants were excluded from the analysis for protocol reasons.

What can be learned from the posted estimates?

The estimates describe the observed outcome summaries and comparisons for the stated populations and timepoints. The confidence intervals and p-values are statistical summaries, not substitutes for the underlying design and analysis details. No alternative adjustment or recalculation is needed to describe the posted estimates, and the registry record does not flag a discrepancy between posted and recalculated results. However, the absent analysis description limits independent evaluation of model appropriateness and reproducibility.

General explanation: statistical significance and precision answer different questions. A p-value addresses compatibility with a null model under analysis assumptions, whereas a confidence interval indicates a range of estimates consistent with the data and method. Neither one addresses whether all relevant outcomes were reported, whether missing observations could affect the result, or how broadly the findings apply. Those questions require information that is not reported in the registry record.

11. Confidence Intervals and Precision

The primary preference comparison has a risk-difference estimate of -0.204, with a 95% confidence interval from -0.334 to -0.073. The interval does not include zero. In general, a confidence interval describes the range of values compatible with the observed data under the method’s assumptions; it is not a guarantee that the true value lies within the particular interval. Its interpretation depends on the validity of the analysis model, and the registry record does not report the model used for this comparison.

The interval indicates uncertainty around the size of the preference contrast, while retaining the negative direction for COSOPT relative to AZARGA throughout its limits. It does not establish that every participant preferred AZARGA, nor that the same proportions would be observed in another population or setting. The primary endpoint is a choice, and the interval concerns the group-level difference in choice proportions rather than individual changes in comfort.

For ocular discomfort, the reported mean difference is 1.1, with a confidence interval from 0.445 to 1.755. This interval also does not include zero. The estimate concerns a difference in average scores, and the standard deviations describe variation in scores within treatment summaries. The scale’s range and direction are not reported, which limits interpretation of the interval in terms of the possible score values or clinical meaning.

Confidence intervals do not address all sources of uncertainty. They do not account automatically for missing data, multiplicity, unreported analysis choices, or possible sequence and period effects in a crossover design. Those issues are not resolved by an interval that excludes zero. The registry record’s lack of analysis detail means the posted intervals can be described numerically, while their dependence on specific modeling choices remains unclear.

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 the observed effects, not the original trial’s design justification. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect set as a stated fraction of the observed effect. The figures are participants per arm, not total event counts. The trial itself used a crossover design, so these hypothetical equal-allocation calculations should not be mistaken for a description of its actual enrollment plan.

The 80% power column gives the number of participants per arm in the planning illustration for an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are prospective planning concepts and do not indicate the probability that the trial’s observed result is true. This is not observed power.

For the primary preference comparison, planning for 100% of the observed effect corresponds to 94 participants per arm for 80% power and 125 participants per arm for 90% power. Planning for 75% of the observed effect corresponds to 167 participants per arm for 80% power and 223 participants per arm for 90% power. Planning for 50% of the observed effect corresponds to 374 participants per arm for 80% power and 500 participants per arm for 90% power. The secondary outcome has its own set of planning illustrations based on its observed mean difference.

Smaller effects are harder to distinguish from random variation, so the planning calculations require more participants per arm when the target effect is reduced. These values rely on the stated assumptions and the observed effect used as their reference. The registry record does not report the original sample-size justification or the assumptions used to plan the completed crossover trial.

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 = 0.602; treatment proportion p₁ = 0.398; average p̄ = 0.500.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7071 = 1.3859.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6923 = 0.5826.
4. n = (1.3859 + 0.5826)² / (-0.2037)² = 93.4, rounded up to 94 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 <- 0.601851851851852                          # control proportion
p1 <- 0.398148148148148                          # 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(1340014)
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 = 94 (80% power), 125 (90% power)
 75% of observed effect: n per arm = 167 (80% power), 223 (90% power)
 50% of observed effect: n per arm = 374 (80% power), 500 (90% power)
power.prop.test: 93.4 
Simulated power at n = 94 per arm: 0.802 (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

The registry record reports two outcome measures and one posted secondary outcome. It gives unadjusted p-values for the primary preference comparison and the secondary ocular-discomfort comparison, but it does not describe a multiplicity strategy, such as a prespecified hierarchy or adjustment for testing more than one outcome. Without that information, the reported p-values should be read as unadjusted and not as evidence that the overall chance of a false-positive conclusion was controlled across all outcomes considered.

The record lists no reported analyses, even though outcome estimates and comparisons are displayed. A detailed statistical analysis plan, including the primary model, treatment of the crossover structure, and any planned sensitivity analyses, is not reported in the registry record. It is therefore not possible to determine from the registry entry whether each posted analysis was prespecified, how the analysis accounted for sequence and period, or whether all planned comparisons are represented.

The primary population is defined as participants who completed both treatment periods and the preference questionnaire, analyzed as treated. The registry reports 108 participants for each treatment in the primary outcome, while total enrollment is 112. The reasons for the difference between enrollment and the primary outcome population are not reported in the registry record. No missing-data method, imputation approach, or sensitivity analysis is described. It is consequently unclear whether missing questionnaires or incomplete periods could have influenced the reported preference distribution.

The secondary outcome also reports 108 participants per treatment. The record does not provide a separate explanation of the analysis population for that outcome or describe how incomplete discomfort measurements were addressed. As this is a crossover trial, the availability of measurements in both periods can matter for paired analyses; the registry record does not explain how partial records were used.

These reporting gaps do not negate the posted estimates, but they limit assessment of their robustness and reproducibility. The values can be described as registry results, while conclusions about multiplicity control, missingness, and the intended analysis population beyond the stated primary definition remain unresolved.

15. 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.

The safety figures list 112 participants at risk for serious adverse events in each treatment group, with zero serious adverse events recorded for AZARGA and zero for COSOPT. The same groups each list 112 participants at risk for other adverse events, with zero recorded in each. These counts should be read as the registry’s reported event figures for the listed groups, not as a complete account of every possible safety outcome.

The registry record does not provide serious adverse event terms, and the top serious adverse event terms list is empty. Death counts are not reported in the registry record. No event durations, severity breakdowns, attribution details, or follow-up beyond the reported treatment periods are described in the available safety information. The record also does not explain how adverse events were assigned in a crossover trial where participants received both medications.

Zero events in the listed data means that no events were recorded in those categories for the reported groups; it does not establish that an event cannot occur or characterize risks outside the study’s observation and reporting. These figures are descriptive and should not be expanded into a broader claim about comparative safety.

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

The primary result answers a focused question: among participants who completed both treatment periods and the questionnaire, which medication did they prefer when asked to consider comfort? The recorded percentages show that AZARGA was selected more often than COSOPT in this analyzed group. The estimated risk difference is negative when expressed as COSOPT relative to AZARGA, and its confidence interval remains negative. This describes the observed preference contrast and its statistical uncertainty under the method used.

The result does not establish that all participants preferred one treatment, that preferences would be the same in other populations, or that preference predicts a clinical outcome. It does not measure disease control, long-term experience, or every aspect of tolerability. The study’s stated question concerns comfort after one week of each medication, and the primary preference response was collected after both periods. Other questions require evidence not reported in this trial record.

The ocular-discomfort outcome supplies a separate numerical comparison at Day 7 of each period. Its results are related to the primary question but remain a distinct measure. Because the scale’s range and direction are not reported, interpretation of its units is limited. Neither outcome alone establishes why participants made their preference choices.

The crossover design allowed participants to experience both medications, but sequence and period can matter when treatment order is involved. The registry record describes randomization to treatment sequences and a 48-hour washout, but does not report an analysis of sequence, period, or carryover effects. Nor does it describe missing-data handling or a multiplicity plan. These limits affect how confidently the estimates can be generalized or assessed as confirmatory evidence.

The posted p-values and confidence intervals are statistical summaries of the recorded comparisons. They do not by themselves establish clinical importance, eliminate the possibility of bias, or resolve reporting gaps. A careful reading keeps the conclusion at the level the trial measured: participant preference and a secondary discomfort score over the specified periods.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a patient-reported preference question with a crossover design. Instead of asking participants to judge only one medication, the study schedule exposed participants to both and then asked for a choice. That design fits a question about relative personal experience, while also creating analysis considerations that are different from those in a standard parallel-group comparison.

The registry record illustrates why the outcome definition matters. Preference is categorical: a participant chooses one option. Ocular discomfort is recorded as a numerical score. These measures can address related aspects of experience, but they do not answer the same question. Agreement in broad direction can be informative descriptively, yet a preference response cannot be treated as a direct substitute for a score, and the score cannot fully explain an individual’s choice.

The posted comparison includes an estimate, confidence interval, and unadjusted p-value, allowing readers to consider both direction and precision rather than relying on a single significance label. The primary interval remains on one side of zero, while the registry record does not give enough analysis detail to reconstruct the model or evaluate all assumptions. This contrast highlights a central statistical lesson: numerical precision and reporting completeness are separate dimensions of evidence.

The record also demonstrates the importance of distinguishing observed study results from planning illustrations. The sample-size figures are based on observed effects and stated generic planning assumptions; they are not the original design justification or a measure of the trial’s achieved power. Keeping those roles separate prevents retrospective calculations from being mistaken for the basis on which the trial was planned.

Finally, the crossover format, restricted questionnaire population, unadjusted secondary result, and limited missing-data reporting all shape the scope of interpretation. These features do not erase the reported findings, but they identify what a statistically careful reader needs before extending them beyond the measured outcomes and observed participants.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

A specific limitation is that the study used a crossover sequence, but the registry record does not report whether the analyses accounted for within-participant pairing, treatment period, treatment order, or possible carryover. The schedule included a 48-hour washout, but its rationale and adequacy are not reported. Without the analysis details, the uncertainty estimates cannot be independently assessed for their treatment of the repeated observations.

The primary outcome includes people who completed both treatment periods and the preference questionnaire. Enrollment was 112, while the primary result reports 108 participants for each treatment. The registry record does not explain the difference, identify reasons for missing outcome data, or describe sensitivity analyses. Selection associated with completing both periods or the questionnaire could limit how representative the analyzed participants are of everyone enrolled.

The preference endpoint is a single question. The record does not report validation information, response options beyond the medication choice, or additional measures of the strength of preference. The secondary discomfort outcome has a mean and standard deviation, but the scale range, anchors, and scoring direction are not reported. This makes it difficult to translate score differences into a clear interpretation of the measurement itself.

The record reports unadjusted p-values but no multiplicity approach, and lists no reported analyses. It does not include the original sample-size justification, a full statistical analysis plan, or a description of who was masked. The study’s short treatment periods and the registry’s limited account of follow-up also constrain conclusions to the recorded timepoints and outcomes.

These are limits in what can be evaluated from the registry record, not proof that a particular design or analysis problem occurred. They indicate why the estimates should be interpreted narrowly and why broader claims require details not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Patient Preference Comparison of AZARGA Versus COSOPT — NCT01340014.
• Registry record last updated 2014-02-10; status last verified 2014-01.
• Results first posted 2013-12-13.
• 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

NCT01340014 is a completed Phase 4 randomized, single-masked crossover trial sponsored by Alcon Research. It enrolled 112 participants with open-angle glaucoma or ocular hypertension and compared AZARGA with COSOPT. Participants received each medication twice a day for 7 days, with a 48-hour washout between periods, in one of two treatment sequences.

The primary outcome was participant preference for comfort, assessed at Day 15 after both treatment periods. The reported preference was 60.2% for AZARGA and 39.8% for COSOPT; the comparison for COSOPT relative to AZARGA was -0.204, with a confidence interval from -0.334 to -0.073 and an unadjusted p-value of 0.003. Ocular discomfort was reported as a secondary outcome at Day 7 of each period.

The registry record does not report the original sample-size justification, a detailed analysis plan, multiplicity handling, or missing-data methods. These omissions limit evaluation of the posted comparisons beyond their stated outcome definitions and populations.