A Safety and Efficacy Study Comparing the Combination Treatments of Verteporfin Therapy Plus One of Two Different Doses of Intravitreal Triamcinolone Acetonide and the Verteporfin Therapy Plus Intravitreal Pegaptanib: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Safety and Efficacy Study Comparing the Combination Treatments of Verteporfin Therapy Plus One of Two Different Doses of Intravitreal Triamcinolone Acetonide and the Verteporfin Therapy Plus Intravitreal Pegaptanib (NCT00242580), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Lose Less Than 15 Letters of Best Corrected Visual Acuity (BCVA) at 12 Months From Baseline..

2. Clinical Question

3. Trial Design

The registry record describes a randomized, quadruple-masked, parallel-group, multicenter phase 3 trial with a planned duration of 24 months. It was sponsored by Novartis Pharmaceuticals, enrolled 111 participants, and is listed as completed. The record lists a start date of 2005-09 and a primary completion date of 2008-01.

Three treatment groups combined verteporfin photodynamic therapy with an intravitreal drug. The groups were verteporfin plus triamcinolone acetonide 1 mg, verteporfin plus triamcinolone acetonide 4 mg, and verteporfin plus pegaptanib. The arm descriptions state that the triamcinolone groups received treatment at baseline and could receive repeat treatment at visits through Month 9 if leakage was detected. The pegaptanib group received treatment at baseline and then every 1.5 months through the 10.5 month visit. The full repeat-treatment schedule for verteporfin is not reported in the registry record.

The primary endpoint was assessed from baseline to Month 12, although the official title describes a 24-month study. That distinction matters: the posted primary result concerns the Month 12 endpoint, not a complete account of outcomes through the full trial duration. The registry record lists six outcome measures and several secondary visual-acuity outcomes, but does not report values for every listed outcome. It also does not report the original sample-size justification, allocation ratio, detailed randomization procedures, or the masking procedures for each study role.

For the primary endpoint, the posted group sizes were 32 participants for verteporfin plus 1 mg triamcinolone, 41 for verteporfin plus 4 mg triamcinolone, and 38 for verteporfin plus pegaptanib. These group sizes correspond to the participants included in the posted endpoint results. The registry record does not give further detail on exclusions or the timing and reasons for missing observations.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) data set includes data from all randomized patients. Missing data were imputed using last observation carried forward.

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 Percentage of Participants Who Lose Less Than 15 Letters of Best Corrected Visual Acuity (BCVA) at 12 Months From Baseline., measured over Baseline to Month 12.

The primary endpoint is the percentage of participants who lost less than 15 letters of best corrected visual acuity from baseline to Month 12. Visual acuity was assessed using the ETDRS chart at a starting distance of 4 meters. The registry record notes that an ETDRS score of 85 is approximately 20/20 and that a decrease in score indicates worsening vision.

This is a binary outcome: each participant is classified according to whether their visual-acuity loss stayed below the specified threshold. The reported percentage therefore describes the share of the analyzed group meeting that outcome, rather than the average change in visual-acuity score. It can be useful for communicating how often a defined degree of loss was avoided within the study’s endpoint definition. It does not describe the size of each participant’s change, distinguish smaller losses from gains, or capture visual function beyond the measured chart score.

The registry record defines the primary analysis population as the intent-to-treat data set, including all randomized patients, and says missing data were imputed using last observation carried forward. That approach affects how participants with missing Month 12 measurements contribute to the endpoint. The record does not report further details about missingness or sensitivity analyses.

7. Results Posted in the Registry

• Verteporfin + 4 mg Triamcinolone: 63.4% (26/41) versus 59.4% (19/32) on control; risk difference 4.0 percentage points (95% CI -18.5 to 26.6), risk ratio 1.07 (0.74–1.54); unadjusted two-proportion z-test p = 0.725.
• Verteporfin + Pegaptanib: 71.1% (27/38) versus 59.4% (19/32) on control; risk difference 11.7 percentage points (95% CI -10.6 to 34.0), risk ratio 1.20 (0.84–1.70); unadjusted two-proportion z-test p = 0.305.

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.

Percentage of Participants With Gain of 5 or More Letters of Best Corrected Visual Acuity From Baseline to Month 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Verteporfin + 4 mg Triamcinolone: 12.2% (5/41) versus 31.2% (10/32) on control; risk difference -19.1 percentage points (95% CI -38.0 to -0.1), risk ratio 0.39 (0.15–1.03); unadjusted two-proportion z-test p = 0.046.
  • Verteporfin + Pegaptanib: 28.9% (11/38) versus 31.2% (10/32) on control; risk difference -2.3 percentage points (95% CI -23.9 to 19.3), risk ratio 0.93 (0.45–1.89); unadjusted two-proportion z-test p = 0.834.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Verteporfin + 4 mg Triamcinolone 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 Verteporfin + Pegaptanib and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Gain of BCVA of 10 or More Letters at 12 Months

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Verteporfin + 4 mg Triamcinolone: 2.4% (1/41) versus 18.8% (6/32) on control; risk difference -16.3 percentage points (95% CI -30.6 to -2.0), risk ratio 0.13 (0.02–1.03); unadjusted two-proportion z-test p = 0.019.
  • Verteporfin + Pegaptanib: 23.7% (9/38) versus 18.8% (6/32) on control; risk difference 4.9 percentage points (95% CI -14.2 to 24.1), risk ratio 1.26 (0.50–3.17); unadjusted two-proportion z-test p = 0.616.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Verteporfin + 4 mg Triamcinolone 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 Verteporfin + Pegaptanib and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Gain of BCVA Score of 15 or More Letters at Month 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Verteporfin + 4 mg Triamcinolone: 0.0% (0/41) versus 6.2% (2/32) on control; risk difference -6.2 percentage points (95% CI -14.6 to 2.1); unadjusted two-proportion z-test p = 0.105.
  • Verteporfin + Pegaptanib: 13.2% (5/38) versus 6.2% (2/32) on control; risk difference 6.9 percentage points (95% CI -6.7 to 20.5), risk ratio 2.11 (0.44–10.13); unadjusted two-proportion z-test p = 0.337.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Verteporfin + 4 mg Triamcinolone 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 Verteporfin + Pegaptanib and the control. The interval gives the range of effects that remain compatible with the data.

The secondary visual-acuity outcomes use progressively larger thresholds for letter gains, alongside the primary endpoint focused on limiting visual-acuity loss. Across the posted gain outcomes, the group pattern is not uniform: the 4 mg triamcinolone group has lower reported percentages than the other groups, while the pegaptanib group and 1 mg triamcinolone group vary in their relative percentages across thresholds. This variation means that a single broad claim about visual-acuity gain would oversimplify the posted results.

The primary endpoint asks whether participants stayed below a defined degree of visual-acuity loss, whereas the secondary gain outcomes ask how many participants achieved specified improvements. These are related but distinct questions. A pattern on a gain threshold cannot replace the primary result, and the primary endpoint does not establish what happened on the gain outcomes. The posted results therefore offer complementary descriptions rather than a single interchangeable measure.

Several secondary comparisons have unadjusted p-values below 0.05, but the registry record does not report a multiplicity adjustment or a complete analysis plan. In general, testing multiple outcomes and contrasts increases the opportunity for apparently notable findings to arise by chance. Without a reported strategy for controlling that issue, individual unadjusted secondary results carry less weight than a prespecified primary analysis and should be treated as exploratory.

The registry record lists additional outcomes concerning verteporfin treatment requirements and change in lesion area, but their results are not reported in the registry record. The secondary evidence is therefore incomplete in the posted record. It provides context for the primary visual-acuity outcome, but does not supply a comprehensive account of all listed outcomes or an adjusted inferential assessment across them.

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

• Percentage of Participants With Gain of 5 or More Letters of Best Corrected Visual Acuity From Baseline to Month 12
• Percentage of Participants With Gain of BCVA of 10 or More Letters at 12 Months
• Percentage of Participants With Gain of BCVA Score of 15 or More Letters at Month 12
• Number of Participants Requiring Verteporfin Treatment Throughout the Study
• Mean Change From Baseline in Total Area of Lesion at 12 Months

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants either met the criterion of losing less than 15 letters by Month 12 or did not. For a binary outcome, the group percentage is the proportion of participants with the event of interest. In general, a risk difference compares those proportions by subtracting one group’s event proportion from another’s. A positive or negative estimate indicates the direction of the observed contrast according to the chosen ordering of groups; it does not by itself establish that the contrast is precise or important.

What does the risk difference compare?

The registry record uses the verteporfin plus 1 mg triamcinolone group as the comparison group for the posted calculations. Each recalculated risk difference therefore contrasts one other group with that reference group for the same endpoint. The displayed group percentages are useful for understanding the observed results, while an interval around a risk difference conveys uncertainty in the contrast. The recalculated comparisons are unadjusted: they use the posted summary outcomes and do not incorporate an adjustment for other variables.

In general, an unadjusted comparison is not necessarily the same as the trial’s planned or sponsor-reported analysis. The registry record lists no reported analyses for these comparisons. The reported analysis plan, including any covariate adjustment or other modeling choices, is not reported in the registry record. The recalculations should therefore be read as descriptive statistical comparisons rather than as a substitute for a trial analysis that is absent from the record.

How should p-values be read?

In general, a p-value measures how compatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not quantify the probability that a treatment is beneficial or harmful. A p-value also does not show whether a difference is clinically important. The unadjusted p-values posted for the primary comparisons are 0.725 and 0.305. Their interpretation is limited by the small group sizes, the absence of a reported sponsor analysis, and the lack of a reported multiplicity plan.

The confidence intervals and p-values address related aspects of uncertainty, but neither should be interpreted in isolation. In general, an interval gives a range of effect estimates compatible with the data under the method used. If an interval for a risk difference includes zero, the data are compatible with no difference as well as with differences in either direction. An interval that is wide indicates limited precision. The primary comparison intervals include zero, which is consistent with the unadjusted p-values.

What does the analysis population mean?

The registry record defines the primary analysis population as intent-to-treat, including all randomized patients. This approach is intended to preserve the comparison created by randomization by analyzing participants in their assigned groups. The record also states that missing data were imputed using last observation carried forward. In general, this method carries a participant’s last recorded value forward to a later assessment when the later value is missing. Its use relies on assumptions about how the unobserved outcome relates to the last observed value; the registry record does not report sensitivity analyses or further assumptions for this imputation.

The methods for the original sample-size calculation, interim analyses, and the trial’s full statistical analysis plan are not reported in the registry record. The separate planning illustrations are calculations based on the observed effect and stated assumptions; they are not evidence of the trial’s original design choices. In general, an observed effect from a small trial can be unstable, so planning calculations based on it should be treated as scenarios rather than reliable estimates of a future effect.

Why does over-dispersion matter?

In general, over-dispersion occurs when the variability in data is greater than a statistical model expects. It can make model-based uncertainty estimates too small if the extra variability is not accounted for. The primary outcome is a binary participant-level percentage, and the registry record does not report an over-dispersion assessment or a model-based sponsor analysis. No claim about over-dispersion can be made from the posted summary percentages alone.

Overall, the posted information permits a basic description of the primary outcome and unadjusted comparisons. It does not establish what inferential method the sponsor planned, whether any additional adjustments were prespecified, or how missing-data assumptions were examined. Those details are not reported in the registry record, so interpretation should remain close to the outcome definition, group percentages, and uncertainty in the recalculated comparisons.

11. Confidence Intervals and Precision

The primary group percentages are 59.4%, 63.4%, and 71.1%. The recalculated risk-difference intervals for both comparisons with the 1 mg triamcinolone group include zero. In practical terms, the posted primary results do not locate either between-group contrast precisely enough to rule out no difference, and the intervals also allow for differences in either direction.

In general, a confidence interval describes the range of values compatible with the observed data under a particular statistical method. It is not a guarantee that the true effect lies within that range, nor does it describe the range of individual participants’ outcomes. A wide interval signals that the estimate is uncertain. With the primary group sizes of 32, 41, and 38, the recalculated intervals are broad, so the data leave substantial uncertainty about the size and direction of the contrasts.

The registry record does not report sponsor-derived confidence intervals for the primary comparisons. The interval interpretation therefore applies to the simple unadjusted recalculations, not to an analysis documented as the trial’s planned method. The intervals also do not address potential multiplicity from evaluating several outcomes or comparisons. A lack of a narrow interval should not be recast as proof that effects are absent, and the numerical ordering of group percentages should not be treated as a precise estimate of a treatment difference.

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 display gives planning illustrations in participants per arm for the binary outcomes reported in this trial. It does not give total event counts. For each comparison, the scenarios use the observed effect, 75% of the observed effect, or 50% of the observed effect. The listed assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the other assumptions hold. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. These are planning targets, not properties of the completed study.

Smaller effects are harder to distinguish from random variation, so the scenarios for a smaller fraction of the observed effect require more participants per arm. The figures depend on the observed effect used as the starting point, which can be uncertain in a trial with small groups. A planning calculation based on an observed effect should not be treated as a guarantee that the same effect will recur in a future study. This is not observed power; it is a set of prospective sample-size illustrations using the stated assumptions.

The sample-size curve can be read as a visual representation of how required enrollment changes with the effect targeted for detection. It should be interpreted alongside the assumptions and the specific comparison, rather than as a universal enrollment recommendation. The figures do not reveal the original trial’s rationale for enrolling 111 participants.

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 = 0.594; treatment proportion p₁ = 0.634; average p̄ = 0.614.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6885 = 1.3494.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6879 = 0.5790.
4. n = (1.3494 + 0.5790)² / (0.0404)² = 2,278.8, rounded up to 2,279 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 <- 0.59375                          # control proportion
p1 <- 0.634146341463415                          # 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(242580)
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 = 2,279 (80% power), 3,051 (90% power)
 75% of observed effect: n per arm = 4,072 (80% power), 5,450 (90% power)
 50% of observed effect: n per arm = 9,204 (80% power), 12,321 (90% power)
power.prop.test: 2278.8 
Simulated power at n = 2,279 per arm: 0.801 (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 trial lists a primary outcome and multiple secondary outcomes, including several visual-acuity gain thresholds. Comparisons are also made between two treatment groups and the 1 mg triamcinolone group. When many outcomes or contrasts are examined, the chance of observing an apparently unusual result somewhere among them can increase. In general, multiplicity methods can control that risk by adjusting the testing strategy or by defining a hierarchy of outcomes and comparisons.

A multiplicity strategy, including whether adjustment was planned or performed, is not reported in the registry record. The posted p-values for secondary outcomes are unadjusted. They should not be interpreted as if they account for all outcomes and comparisons in the trial. The record also does not report the complete statistical analysis plan, prespecified analysis hierarchy, or interim analyses.

For the primary endpoint, the registry record specifies an intent-to-treat population including all randomized patients and says missing data were imputed using last observation carried forward. It does not report how many outcome values were missing, the timing or reasons for missingness, or sensitivity analyses assessing alternative assumptions. In general, carrying the last observed value forward treats that value as an estimate of the later missing measurement; this may not reflect what would have been observed. The effect of that assumption cannot be judged from the information reported.

The record lists six outcome measures, but results for every listed outcome are not reported in the registry record. The detailed statistical methods used by the sponsor, including any adjustments or model specifications, are also not reported. Consequently, recalculated unadjusted comparisons are useful for understanding the posted summaries but cannot resolve questions about prespecification, selective reporting, or robustness to missing-data assumptions.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: accidental injury (7.9%), gastrointestinal disorder (5.3%), pneumonia (5.3%), coronary artery disorder (4.9%), cerebral infarct (4.9%).

The registry record reports serious adverse events in 11 of 32 participants in the verteporfin plus 1 mg triamcinolone group, 9 of 41 in the verteporfin plus 4 mg triamcinolone group, and 10 of 38 in the verteporfin plus pegaptanib group. For other adverse events, the reported affected-participant counts are 32 of 32, 38 of 41, and 30 of 38, respectively. These counts describe participants recorded as affected; they do not indicate how many separate events each participant experienced or their duration.

The listed serious-event terms include accidental injury at 7.9%, gastrointestinal disorder at 5.3%, pneumonia at 5.3%, coronary artery disorder at 4.9%, cerebral infarct at 4.9%, and anaphylactoid reaction at 3.1%. The registry record does not provide further detail in the registry record about the definitions, severity grading, timing, or causal attribution of these terms. Death counts are not reported in the registry record.

These figures should be read as descriptive safety information for the trial groups, not as proof that an event was caused by a treatment or that the groups differ in risk. Group sizes are limited, and the record does not report a comparative safety analysis.

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

The posted primary data show that the percentage meeting the Month 12 criterion of losing less than 15 letters was 59.4% with verteporfin plus 1 mg triamcinolone, 63.4% with verteporfin plus 4 mg triamcinolone, and 71.1% with verteporfin plus pegaptanib. The unadjusted recalculated comparisons have intervals that include no difference. These results describe the participants and endpoint recorded; they do not establish that one regimen is superior, equivalent, or inferior to another.

A difference in group percentages is not automatically a reliable estimate of a treatment effect. Random variation can be substantial with limited group sizes, and uncertainty is reflected in the broad comparison intervals. The absence of a precise contrast does not prove that the true effects are identical. Conversely, a numerical difference does not establish that a meaningful difference exists.

The primary outcome is a threshold-based visual-acuity measure at Month 12. It does not show the full distribution of visual-acuity changes, explain changes in other aspects of vision, or establish outcomes across the complete 24-month study duration. The registry record lists other outcomes, but results for all listed measures are not reported. The primary population also used last observation carried forward for missing data, and the record does not provide sensitivity analyses that would show how results might vary under other assumptions.

The secondary results add context but include multiple unadjusted comparisons, with no multiplicity strategy reported. They should not be used to make a stronger claim than the primary endpoint supports. The safety counts are likewise descriptive and do not establish causation or a comparative safety profile. Overall, the posted record offers a limited statistical account of the trial’s Month 12 outcomes, rather than a complete basis for conclusions about treatment effects or longer-term outcomes.

17. Why This Trial Matters Statistically

This trial illustrates why a group percentage and a treatment comparison answer different questions. The percentages describe the observed share of participants meeting the endpoint in each group. A risk difference estimates the contrast between groups, while its confidence interval communicates how uncertain that contrast is. Here, the primary percentages vary across the three groups, but the recalculated intervals include no difference. Reading only the percentages would therefore overstate the certainty of the comparison.

It also illustrates how the endpoint definition shapes interpretation. The primary outcome is not average visual-acuity change; it is the percentage below a threshold of loss. Secondary outcomes examine gains at different thresholds, which are related but not equivalent measures. Results can vary across these definitions without any one measure capturing the whole visual-acuity profile.

The registry record makes the analysis-population and missing-data approach explicit for the primary outcome: intent-to-treat with last observation carried forward. At the same time, it does not report a full analysis plan, sponsor analyses for the comparisons, or a multiplicity strategy. That combination shows why readers should distinguish what the record states from what remains uncertain, rather than filling in methodological details by assumption.

Finally, planning illustrations based on observed effects are not the same as the trial’s original design justification. They can show how enrollment requirements change under stated scenarios, but cannot establish what assumptions guided the completed study. Together, these points make the record useful for learning how endpoint definitions, precision, missing data, and multiplicity affect interpretation of a randomized clinical trial.

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.

The registry record provides primary group percentages and supports simple unadjusted comparisons, but it lists no sponsor-reported analyses for those comparisons. The recalculated estimates therefore do not stand in for a documented primary statistical analysis. The analysis plan, including any covariate adjustment, model specifications, or prespecified comparison hierarchy, is not reported in the registry record.

The primary endpoint is measured at Month 12 in a study described as lasting 24 months. The available primary outcome does not establish what happened at later time points. Although additional outcomes are listed, results for the verteporfin-treatment requirement and lesion-area outcomes are not reported in the registry record. Nor does the record provide a complete result set for every listed measure.

The primary analysis uses last observation carried forward for missing data, but the number and pattern of missing measurements and sensitivity analyses are not reported. This limits assessment of how the imputation choice may affect the result. The posted arm sizes are modest, and the primary comparison intervals are broad, limiting precision.

The registry record also does not report the original sample-size justification, allocation ratio, interim analyses, detailed randomization procedures, or detailed masking procedures. It gives serious and other adverse-event counts but not a comparative safety analysis, event timing, or causal attribution. These limitations mean that the record supports a bounded description of the posted outcomes, not a complete appraisal of all trial methods or results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Safety and Efficacy Study Comparing the Combination Treatments of Verteporfin Therapy Plus One of Two Different Doses of Intravitreal Triamcinolone Acetonide and the Verteporfin Therapy Plus Intravitreal Pegaptanib — NCT00242580.
• Registry record last updated 2016-03-31; status last verified 2016-03.
• Results first posted 2011-05-02.
• 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

This completed randomized, quadruple-masked, parallel-group, multicenter phase 3 trial enrolled 111 participants with subfoveal choroidal neovascularization secondary to age-related macular degeneration. It compared verteporfin photodynamic therapy combined with intravitreal triamcinolone acetonide 1 mg, triamcinolone acetonide 4 mg, or pegaptanib.

The primary outcome was the percentage of participants who lost less than 15 letters of best corrected visual acuity from baseline to Month 12. The posted percentages were 59.4%, 63.4%, and 71.1%, respectively. Unadjusted recalculated comparisons have intervals that include no difference; the registry record lists no sponsor-reported analyses for these comparisons.

The record specifies an intent-to-treat primary population and last observation carried forward for missing data. It does not report the original sample-size justification, a multiplicity strategy, or a complete statistical analysis plan. Results for some listed secondary outcomes are not reported in the registry record.