Macular EpiRetinal Brachytherapy Versus Lucentis® Only Treatment (MERLOT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Macular EpiRetinal Brachytherapy Versus Lucentis® Only Treatment (MERLOT) (NCT01006538), a randomized phase 4 study. The primary outcome is Mean Change in Early Treatment for Diabetic Retinopathy Study (ETDRS) Best-corrected Visual Acuity (BCVA) From Baseline to Month 12.

2. Clinical Question

The question is specifically about adding a focal radiation procedure to ongoing, as-needed ranibizumab for a population already receiving anti-VEGF treatment. It is not a comparison of brachytherapy alone with ranibizumab, and it does not address starting treatment in people who have not previously received anti-VEGF therapy. Both arms could receive ranibizumab according to the retreatment criteria, so the contrast concerns the treatment strategies recorded for the two arms rather than exposure to ranibizumab versus no ranibizumab.

3. Trial Design

MERLOT, registered as NCT01006538, was a phase 4 randomized controlled trial with a parallel-group design and single masking. The sponsor was King's College Hospital NHS Trust. The record lists enrollment as 363 and the trial status as completed. The recorded start was 2009-11, and primary completion was 2015-03. The registry record does not describe the allocation sequence or identify which roles were masked.

The treatment arm received a single procedure of epimacular brachytherapy using the VIDION® System, with Lucentis® (0.5 mg) administered monthly as required. The control arm received Lucentis® (0.5 mg) monthly as required, using the retreatment criteria described in the record. The posted primary-outcome group sizes were 244 for the combination arm and 119 for the Lucentis-only arm. The registry record does not report why these outcome group sizes differ, whether all randomized participants contributed to the primary analysis, or how missing month-12 measurements were handled.

The primary endpoint was mean change in ETDRS best-corrected visual acuity from baseline to month 12. Secondary outcomes listed in the record include thresholds for losing or gaining ETDRS letters and changes in lesion size, choroidal neovascular membrane size, and foveal thickness. The record lists eight outcome measures, but only some secondary results are included in the posted figures; it lists no reported analyses for the outcomes. A full statistical analysis plan, the original sample-size justification, interim-analysis arrangements, and detailed analysis-population definitions are not reported in the registry record.

The trial targets a particular clinical context: people who had already commenced anti-VEGF therapy and were described as requiring frequent injections. Its randomized comparison therefore addresses the incremental role of adding a procedure within ongoing ranibizumab treatment, as recorded, rather than the broader question of which initial treatment to choose for all people with wet age-related macular degeneration.

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

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 Mean Change in Early Treatment for Diabetic Retinopathy Study (ETDRS) Best-corrected Visual Acuity (BCVA) From Baseline to Month 12, measured over 12 months.

The primary endpoint is mean change in ETDRS best-corrected visual acuity (BCVA) from baseline to month 12, measured in ETDRS letters. A change score expresses how the measured visual acuity at follow-up differs from the participant's baseline measurement. The reported group means are -4.8 letters for epimacular brachytherapy plus Lucentis® and -0.9 letters for Lucentis® only. The comparison is a difference between these mean changes, not a comparison of final month-12 visual acuity alone.

The registry describes standardized visual acuity testing using ETDRS charts, with testing at 4 meters and, when vision was sufficiently reduced, at 1 meter. The charts and testing protocol are intended to provide a structured way to quantify visual acuity, including in participants with reduced vision. The measure is continuous: it retains the size and direction of change rather than reducing each participant's result to a category such as improved or not improved.

Using a continuous outcome can make it possible to compare average changes across randomized groups while retaining information about the scale of individual measurements. The average does not show the full spread of participants' experiences, however. It does not indicate how many participants improved, remained stable, or declined by a particular amount; the separate secondary outcomes address some such thresholds. Nor does a group mean establish the result for any individual. The registry record does not report a minimal clinically important difference or a prespecified threshold for interpreting the primary mean difference as clinically important.

7. Results Posted in the Registry

• Arm B: Lucentis® Only: mean -0.90 versus -4.80 on control; difference 3.90 (95% CI 1.69 to 6.11), standardized effect d = 0.37; z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Subjects Losing < 15 ETDRS Letters

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: Lucentis® Only: 92.4% (110/119) versus 83.6% (204/244) on control; risk difference 8.8 percentage points (95% CI 2.2 to 15.5), risk ratio 1.11 (1.03–1.19); unadjusted two-proportion z-test p = 0.021.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Arm B: Lucentis® Only than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Subjects Gaining ≥ 0 ETDRS Letters

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: Lucentis® Only: 46.2% (55/119) versus 37.3% (91/244) on control; risk difference 8.9 percentage points (95% CI -1.9 to 19.7), risk ratio 1.24 (0.96–1.60); unadjusted two-proportion z-test p = 0.104.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B: Lucentis® Only and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Subjects Gaining ≥ 15 ETDRS Letters

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: Lucentis® Only: 5.0% (6/119) versus 1.2% (3/244) on control; risk difference 3.8 percentage points (95% CI -0.4 to 8.0), risk ratio 4.10 (1.04–16.11); unadjusted two-proportion z-test p = 0.028.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B: Lucentis® Only and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several related but distinct features: threshold-based changes in ETDRS letters, lesion and choroidal neovascular membrane size, and foveal thickness. The posted threshold results do not all point in the same direction, and the estimates differ in precision. This broad pattern is a reason to treat the secondary outcomes as complementary information rather than as a single consistent verdict about visual acuity or ocular structure.

These outcomes relate to the primary result because they provide other ways of describing visual change and disease-related measurements. The primary endpoint summarizes average change in ETDRS letters, whereas threshold outcomes count participants meeting particular categories. A group difference in an average does not require the same pattern at every threshold: a mean can be influenced by the size of changes across participants, while a threshold count depends on how many fall on one side of a cutoff. The structural outcomes measure different features again and cannot be assumed to mirror visual-acuity change.

Only some secondary results are posted in the record used for these comparisons. The record lists six secondary outcomes and eight outcome measures overall, but it contains no reported analyses for the secondary results. It does not report a prespecified hierarchy among outcomes, a multiplicity correction, or a complete analysis plan. Because multiple outcomes are considered, unadjusted secondary comparisons carry less weight than the primary endpoint: a notable result can arise by chance among many comparisons, and the available record does not show how testing was organized or interpreted by the trial investigators.

The appropriate role of these outcomes is therefore to add context and generate questions, not to overturn or independently confirm the primary result. They can indicate whether the observed pattern merits further study, but cannot alone establish a unified treatment effect across different measures. Missing analysis details and the absence of a reported multiplicity strategy make cautious, non-definitive interpretation especially important.

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

• Percentage of Subjects Losing < 15 ETDRS Letters
• Percentage of Subjects Gaining ≥ 0 ETDRS Letters
• Percentage of Subjects Gaining ≥ 15 ETDRS Letters
• Change in Total Lesion Size by Fluorescein Angiography From Baseline to Month 12
• Change in Total Choroidal Neovascular Membrane (CNV) Size by Fluorescein Angiography From Baseline to Month 12
• Foveal Thickness Measured Using Optical Coherence Tomography (OCT) From Baseline to Month 12

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result compares mean changes in a continuous outcome. Each participant's change is measured from baseline to month 12, and the group mean summarizes those participant-level changes. A mean difference then contrasts the two group averages. In the posted comparison, the difference is defined as Lucentis® only minus epimacular brachytherapy plus Lucentis®. That direction matters: a positive estimate means the control-arm mean change was higher than the treatment-arm mean change. The estimate is 3.9 ETDRS letters.

What does the standard deviation describe?

The standard deviation describes how spread out the individual changes are around a group mean. The posted standard deviations are 10.8 letters in the combination arm and 9.7 letters in the Lucentis-only arm. A standard deviation is a feature of the participant measurements, not a measure of uncertainty in the estimated mean difference. The standard error and confidence interval address uncertainty in the group estimate and comparison. A group can have substantial variation among participants while its mean difference is estimated with greater or lesser precision, depending on the amount of information and the variability in the data.

How should the confidence interval be understood?

A confidence interval describes the uncertainty associated with an estimate under the statistical method used. The primary mean difference is 3.9 letters, and its interval runs from 1.692 to 6.108. Values nearer the estimate are generally more compatible with the data under the model than values far from it, but the interval is not a guarantee that the true effect lies inside it. It also does not account automatically for biases, missing data, selective reporting, or choices made outside the calculation. The registry record does not report an adjusted analysis or the original analysis plan, so the posted interval should be understood as an unadjusted recalculation based on the available summary statistics.

What does the p-value add?

The unadjusted p-value is p < 0.001. In general, a p-value assesses how unusual data at least this discrepant from a specified null model would be if the null model and the assumptions of the test were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. It does not address whether the outcome was measured completely or whether the analysis population and assumptions were appropriate. A p-value should be considered alongside the estimate, its confidence interval, trial design, and reporting context.

Why does randomization matter?

Random allocation is intended to create groups that are comparable on average at the point of assignment, including on factors that are not measured. This supports a causal interpretation of a between-group contrast when the trial is conducted and analyzed appropriately. Randomization does not guarantee that the groups are identical, prevent missing outcomes, ensure adherence, or remove bias from outcome assessment and analysis. The record says the trial was randomized and single-masked, but the sequence-generation method, concealment details, identity of masked roles, and analysis population are not reported in the registry record.

Why can outcome spread and sample size affect precision?

In general, estimates become more precise when the observed data contain more information about the quantity being estimated. For a continuous measure, both the number of observations and the variability of outcomes contribute to the uncertainty in a mean comparison. Greater variation makes it harder to distinguish a group difference from random variation. The observed standard deviations describe variation in this trial; they do not reveal whether the trial's original design assumptions were met. The original sample-size justification and design assumptions are not reported in the registry record.

What is the status of the secondary comparisons?

The secondary outcomes include binary thresholds for losing or gaining specified numbers of ETDRS letters, as well as ocular measurements. Binary outcomes classify participants according to whether a threshold was met, then compare the resulting group proportions. A risk difference is an absolute contrast between proportions; its confidence interval describes uncertainty in that contrast. These measures answer different questions from the primary continuous mean change. The registry record lists no reported analyses for the secondary outcomes, so the posted unadjusted calculations should not be mistaken for a prespecified, fully documented statistical analysis.

When many outcomes or comparisons are examined, some may appear notable by chance even if there is no underlying difference. This is the general problem of multiplicity. The registry record does not report a multiplicity adjustment, a hierarchy of endpoints, or a prespecified testing strategy. Consequently, unadjusted secondary p-values are exploratory evidence rather than a set of independent confirmations. The primary endpoint remains the main result for the stated trial question, while the secondary endpoints offer supporting context that requires cautious interpretation.

These explanations describe general statistical concepts. They do not establish which particular model, missing-data method, or adjustment strategy was used in the trial, because those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary mean difference is 3.9 ETDRS letters, with a 95% confidence interval from 1.692 to 6.108. The interval is entirely above zero, and the unadjusted p-value is p < 0.001. In the direction used for the comparison, the interval is compatible with a higher mean change in the Lucentis-only group than in the brachytherapy-plus-Lucentis group. The interval communicates uncertainty around the estimated average contrast; it does not describe the range of individual participant outcomes.

The endpoints of the interval are not symmetrical when expressed to the displayed decimal precision around the estimate. They should be quoted as posted rather than treated as exact boundaries. The interval is also conditional on the assumptions and data used for the unadjusted recalculation. It does not incorporate uncertainty about choices that are not documented in the registry record, such as handling of missing measurements or adjustments for other variables. The record does not report a sponsor-reported primary analysis to compare with the recalculation.

Precision and clinical importance are different considerations. A comparatively narrow interval can indicate that the statistical estimate is more tightly constrained than an imprecise estimate, but it does not establish that the magnitude is meaningful to participants. The registry record does not report a minimal clinically important difference for ETDRS letters. The interval also does not show how many participants had outcomes better or worse than the group means; that requires participant-level distributions or separately reported threshold outcomes.

The posted standard deviations, 10.8 letters in the combination arm and 9.7 letters in the Lucentis-only arm, describe outcome variability. They help put the mean comparison in context but are not substitutes for the confidence interval. The outcome summaries alone cannot establish whether the model assumptions were checked or whether alternative analyses would produce similar uncertainty estimates. Accordingly, the interval is informative about the posted unadjusted comparison, but it should be read with the trial's reporting gaps in mind.

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 effect, not the trial's original design calculations. For this continuous primary outcome, the figures are participants per arm. The stated illustration assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The registry record does not report the trial's own original sample-size assumptions or justification.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding illustrative number per arm for a higher planned chance of detection. These are design calculations, not statements about the chance that the trial's result is true. This is not observed power.

Rows for planning at 100%, 75%, and 50% of the observed effect illustrate how the target effect changes the required sample size. Smaller effects are harder to distinguish from random variation, so the planning figures increase as the effect to detect becomes smaller. The sample-size table and curve are best read as conditional illustrations: they show what the calculation implies under its assumptions, not what the trial necessarily planned or achieved.

Equal allocation is an assumption for the illustration; the posted primary-outcome group sizes are 244 and 119. The planning calculations should not be used to infer the trial's original allocation plan, justify its achieved enrollment, or judge its observed result as adequately or inadequately powered. They answer a different question: what per-arm sample size a hypothetical design would require for a chosen fraction of the observed effect, under the listed assumptions.

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 = 3.900; pooled standard deviation σ = 10.453.
2. n = 2 × (1.96 + 0.842)² × 10.453² / 3.900² = 112.8, rounded up to 113 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 <- 3.9                      # observed difference in means
sigma <- 10.4531854414134                     # 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(1006538)
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 = 113 (80% power), 151 (90% power)
 75% of observed effect: n per arm = 201 (80% power), 269 (90% power)
 50% of observed effect: n per arm = 452 (80% power), 604 (90% power)
power.t.test: 113.7 
Simulated power at n = 113 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcome measures, including the primary visual-acuity measure and secondary visual-acuity thresholds and ocular measurements. It does not report a testing hierarchy, a designated order for interpreting endpoints, or a method for controlling the chance of false-positive findings across multiple comparisons. It also lists no reported analyses. The posted secondary comparisons are therefore best treated as unadjusted and exploratory rather than as confirmatory tests with a documented family-wise testing strategy.

Multiplicity matters because considering many outcomes creates more opportunities for an apparently unusual result to occur by chance. In general, an adjustment or a prespecified hierarchy can help interpret a collection of tests, but it can also affect the threshold or strategy used for inference. Which approach, if any, was planned or used is not reported in the registry record. The unadjusted p-values should not be read as if each were the sole planned test.

Missing-data handling is also not reported in the registry record. It does not state how participants without a month-12 measurement were handled, whether any measurements were imputed, or whether sensitivity analyses assessed the effect of missing outcomes. The posted primary group sizes are 244 and 119, while enrollment is recorded as 363; those figures alone do not establish which participants were randomized, analyzed, or missing an outcome. The record does not explain the relationship between enrollment and the endpoint analysis groups.

The record does not specify whether the primary analysis followed intention-to-treat principles, included only participants with available measurements, or used another population definition. It does not report how treatment discontinuation, non-adherence, crossover, or other protocol deviations were handled. The registry record also does not provide a detailed statistical analysis plan or say whether any interim analyses were conducted. These omissions limit assessment of whether the posted comparisons reflect prespecified methods and how robust they are to alternative assumptions.

These gaps do not invalidate the posted numbers, but they limit the inferences that can be drawn from them. The primary comparison is more central to the stated question than the secondary results, while conclusions about completeness, analysis choices, and multiplicity remain unsettled by the registry record.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: retinal detachment (1.2%), postoperative uveitis (0.8%), endophthalmitis (0.4%), visual hallucinations (0.4%).

The posted serious adverse event figures are 7 in the epimacular-brachytherapy-plus-Lucentis® group, with 244 at risk, and 0 in the Lucentis-only group, with 119 at risk. The record lists deaths as 3 in the combination group and 5 in the Lucentis-only group. These are descriptive counts; they do not by themselves establish that treatment caused an event or that one strategy is safer.

The listed serious-event terms and percentages are retinal detachment at 1.2%, postoperative uveitis at 0.8%, endophthalmitis at 0.4%, and visual hallucinations at 0.4%. The registry record does not provide enough detail in these figures to determine event timing, duration, severity beyond the serious-event classification, recurrence, or the relationship of each event to treatment. The percentages should be read as reported and not converted into participant counts or assumed to share a denominator beyond what the record explicitly states.

Other adverse events are recorded for 244 participants at risk and 244 affected in the combination group, and for 119 at risk and 50 affected in the Lucentis-only group. These broad counts do not describe event types or severity. Comparisons of safety require fuller information about event definitions, exposure, follow-up, and attribution, which is not reported in the registry record. The figures are signals to interpret cautiously, not a standalone balance of benefits and harms.

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

The posted primary outcome compares average change in ETDRS BCVA between two randomized strategies for people with wet age-related macular degeneration who had commenced anti-VEGF therapy. The mean change was -4.8 letters with epimacular brachytherapy plus as-needed Lucentis® and -0.9 letters with as-needed Lucentis® alone. The unadjusted mean difference was 3.9 letters in the direction of a higher mean change in the Lucentis-only arm, with a 95% confidence interval from 1.692 to 6.108.

This result does not say what happened to every participant. Group averages can conceal a wide range of individual changes, and the posted standard deviations indicate variation within both arms. Nor does a mean change alone describe how many participants met particular improvement or loss thresholds. The threshold-based secondary outcomes address related but different questions and require cautious interpretation because the record does not report a multiplicity strategy.

The result does not establish whether the procedure reduced the need for ongoing injections. Although reducing retreatment frequency motivated the study, the primary endpoint is visual-acuity change, and the registry record does not post an injection-frequency result in the outcomes summarized. The result also does not determine the comparative safety of the two strategies; the adverse-event counts require context about event definitions, follow-up, and attribution.

The trial's population is important to the scope of the inference. The study describes participants who had already commenced anti-VEGF therapy and who required frequent injections. Its findings should not automatically be generalized to untreated disease, to all people with wet age-related macular degeneration, or to treatment settings that differ from the recorded strategies. The registry record does not report subgroup analyses that would clarify variation in results across participant characteristics.

Statistical evidence and clinical meaning are separate. The confidence interval and unadjusted p-value describe the primary comparison under the calculation used, but the registry record does not state a minimal clinically important difference or provide all the analysis details needed to assess sensitivity to missing data or other choices. The posted result is evidence about the average month-12 change in this trial, not a recommendation for an individual and not a complete account of treatment burden, safety, or longer-term outcomes.

17. Why This Trial Matters Statistically

This trial is statistically informative because it tests an added procedure against continued as-needed ranibizumab in a population already receiving anti-VEGF treatment. That is a narrower question than comparing initial treatments in untreated disease. The distinction matters: estimates from one treatment context cannot simply be assumed to apply to another, and the trial's stated population makes its intended comparison explicit.

The primary endpoint is continuous, retaining information about the magnitude and direction of visual-acuity change rather than reducing the outcome to a single threshold. The mean difference and confidence interval provide a direct summary of the average contrast and its statistical uncertainty. The posted estimates show why it is useful to report both group means and a between-group comparison: the comparison's direction and magnitude are clearer when the two arms are considered together.

The trial also illustrates why a statistically clear comparison does not settle every interpretive question. The p-value and confidence interval do not establish clinical importance, individual benefit, injection burden, or safety. Secondary outcomes span threshold-based and structural measures, but their unadjusted status and the lack of a reported multiplicity strategy limit how strongly they can reinforce a conclusion. Missing analysis-population and missing-data details also affect confidence in the completeness of the posted comparison.

For biostatisticians and clinical researchers, the record is a useful reminder to distinguish the estimand implied by a randomized treatment contrast from the outcome actually reported, and to distinguish a registry summary from a complete statistical report. The result is most informative when read together with the specified population, treatment strategies, endpoint, uncertainty, and reporting gaps. Those distinctions help prevent a narrow average-outcome comparison from being interpreted as a broader claim about all aspects of care.

18. Limitations

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

The registry record leaves several trial-specific uncertainties. It does not report the allocation concealment method, the randomization sequence, or which participants or staff were masked. Although the trial is described as single-masked, the masked role is not identified. These omissions make it difficult to assess fully how allocation and outcome assessment were protected from bias.

The primary outcome summaries have different group sizes, but the record does not explain the analysis population or the relationship between those figures and randomized enrollment. It does not report how missing month-12 measurements were handled, whether participants were analyzed according to assigned group, or whether sensitivity analyses were performed. The record also does not describe adherence, treatment discontinuation, or protocol deviations in relation to the primary estimate.

The posted primary comparison is an unadjusted recalculation from summary statistics, and the record lists no reported analyses. No adjusted estimate or detailed analysis plan is reported. This leaves uncertainty about model choices, covariate adjustment, assumption checking, and whether the posted calculation matches the trial's prespecified analysis. The original sample-size justification and trial-specific design assumptions are also not reported; planning illustrations based on the observed effect cannot fill that gap.

For secondary outcomes, the registry record does not describe a multiplicity strategy, a hierarchy of endpoints, or a complete set of analyses. Several listed outcomes do not have posted results in the record. The available information also does not provide participant-level distributions, subgroup estimates, or a reported minimal clinically important difference for the primary visual-acuity measure.

Finally, the primary comparison is at month 12. The registry record does not provide a longer-term primary comparison in the registry record, nor does the posted primary endpoint quantify injection frequency. Safety counts lack detail on timing, exposure, attribution, and event-level context. These limitations restrict interpretation of durability, treatment burden, and comparative safety, even though the randomized design provides a structured basis for the primary between-group comparison.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Macular EpiRetinal Brachytherapy Versus Lucentis® Only Treatment (MERLOT) — NCT01006538.
• Registry record last updated 2020-12-07; status last verified 2019-05.
• Results first posted 2019-07-22.
• 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

MERLOT (NCT01006538) was a completed phase 4 randomized, single-masked, parallel-group trial sponsored by King's College Hospital NHS Trust. It compared a single epimacular brachytherapy procedure plus as-needed Lucentis® with as-needed Lucentis® alone in people with wet age-related macular degeneration who had commenced anti-VEGF therapy.

The primary endpoint was mean change in ETDRS BCVA from baseline to month 12. The posted means were -4.8 letters for the combination arm and -0.9 letters for the Lucentis-only arm. The unadjusted recalculated mean difference was 3.9 letters, with a 95% confidence interval from 1.692 to 6.108 and p < 0.001. The registry record does not report the original sample-size justification, analysis population, missing-data methods, or a multiplicity strategy.