Anti-angiOpoeitin 2 Plus Anti-vascular eNdothelial Growth Factor as a therapY for Neovascular Age Related Macular Degeneration: Evaluation of a fiXed Combination Intravitreal Injection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Anti-angiOpoeitin 2 Plus Anti-vascular eNdothelial Growth Factor as a therapY for Neovascular Age Related Macular Degeneration: Evaluation of a fiXed Combination Intravitreal Injection (NCT02713204), a randomized phase 2 study. The primary outcome is Change From Baseline in Best Corrected Visual Acuity (BCVA) Measured by Early Treatment Diabetic Retinopathy Study (ETDRS) Letter Score at Week 12.

2. Clinical Question

3. Trial Design

This was a randomized, quadruple-masked, parallel-group, active-controlled phase 2 study sponsored by Regeneron Pharmaceuticals. It is marked completed in the registry. The recorded study start was 2016-03-31, and primary completion was 2017-10-03. The reported enrollment was 365. These registry entries describe the study structure, but do not by themselves establish the size or precision of each endpoint analysis.

The study compared repeated intravitreal doses of REGN910-3 with intravitreal aflibercept injection. The primary Week 12 results are given for REGN910-3 at 3 mg:2 mg, REGN910-3 at 6 mg:2 mg, and IAI 2 mg. All groups began with injections every 4 weeks on Day 1, Week 4, and Week 8. The 3 mg:2 mg REGN910-3 group then followed an every-8-week schedule beginning at Week 16. In the 6 mg:2 mg group, participants were re-randomized at Week 12 to later dosing schedules. The registry also describes re-randomization and subsequent schedules for the IAI group.

Re-randomization and schedule changes matter when interpreting later outcomes: the Week 36 groups represent different treatment sequences, rather than a simple continuation of the original Week 12 comparison. The registry record does not report the original sample-size assumptions or a full statistical analysis plan. It also does not report enough information in the record to reconstruct every aspect of allocation concealment, masking procedures, or the reasons for missing measurements.

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: Out of 560 participants, 365 were randomized \& treated. Participants were randomized in 1:2:3 to receive REGN910-3 3:2mg, REGN910-3 6:2mg \& 2mg intravitreal aflibercept injection (IAI) followed by re-randomization at week 12 in REGN910-3 6:2mg \& IAI 2mg arm. Not all participants who completed Week 12 were re-randomized \& continued to Week 36.

Only the first 6 of 8 groups are shown.

Baseline (Day 1) up to Week 12

Reasons for not completing this period:

From Week 12 up to Week 36

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set included all randomized participants who received any study drug, had baseline measurement of BCVA \& at least 1 post-baseline assessment of BCVA. Last observation carried forward (LOCF) method was used to impute missing data. Here "Overall Number of Participants Analyzed" = Participants who were evaluable for this outcome measure.

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 Change From Baseline in Best Corrected Visual Acuity (BCVA) Measured by Early Treatment Diabetic Retinopathy Study (ETDRS) Letter Score at Week 12, measured over At Week 12.

The primary endpoint was change from baseline in best corrected visual acuity (BCVA) at Week 12, measured using the Early Treatment Diabetic Retinopathy Study (ETDRS) letter score. Participants read an eye chart at a testing distance of 4 meters, and the score records the number of letters read correctly. The registry describes the scale as ranging from 0 to 100 letters. A higher score indicates that more letters were read correctly; an increase from baseline therefore represents an improvement in the measured visual acuity.

Change was calculated by subtracting the baseline score from the observed post-baseline score at Week 12. A change score gives an outcome that can be compared across groups while retaining the scale’s direct interpretation in letters correctly read. Visual acuity is a functional measure relevant to the study’s stated objective, while imaging measures such as retinal thickness and lesion area capture different aspects of the eye.

The primary outcome is reported as a mean and standard deviation in each group. Means convey the average change, while standard deviations describe variability among participants. The registry states that missing BCVA values were imputed using last observation carried forward (LOCF). It defines the full analysis set as randomized participants who received any study drug and had baseline and at least one post-baseline BCVA assessment. The registry record does not report further details about the assumptions supporting this imputation.

7. Results Posted in the Registry

• REGN910-3 (6 mg:2 mg): mean 5.60 versus 5.20 on control; difference 0.40 (95% CI -2.87 to 3.67), standardized effect d = 0.04; z-test p = 0.811.
• Aflibercept (IAI) 2 mg: mean 5.40 versus 5.20 on control; difference 0.20 (95% CI -2.84 to 3.24), standardized effect d = 0.02; z-test p = 0.897.

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.

Change From Baseline in Central Sub-field Retinal Thickness (CST) Measured by Spectral Domain Optical Coherence Tomography (SD-OCT) at Week 12

• 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:
  • REGN910-3 (6 mg:2 mg): mean -200.00 versus -182.20 on control; difference -17.80 (95% CI -69.55 to 33.95), standardized effect d = -0.11; z-test p = 0.500.
  • Aflibercept (IAI) 2 mg: mean -178.60 versus -182.20 on control; difference 3.60 (95% CI -44.87 to 52.07), standardized effect d = 0.02; z-test p = 0.884.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between REGN910-3 (6 mg:2 mg) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept (IAI) 2 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Central Sub-field Retinal Thickness (CST) Measured by Spectral Domain Optical Coherence Tomography (SD-OCT) at Week 36

• 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:
  • REGN910-3 (6 mg:2 mg) Q4 to REGN910-3 (6 mg:2 mg) Q8: mean -216.60 versus -174.60 on control; difference -42.00 (95% CI -106.61 to 22.61), standardized effect d = -0.24; z-test p = 0.203.
  • REGN910-3 (6 mg:2 mg) Q4 to REGN910-3 (6 mg:2 mg) Q12: mean -181.30 versus -174.60 on control; difference -6.70 (95% CI -63.08 to 49.68), standardized effect d = -0.04; z-test p = 0.816.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between REGN910-3 (6 mg:2 mg) Q4 to REGN910-3 (6 mg:2 mg) Q8 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 REGN910-3 (6 mg:2 mg) Q4 to REGN910-3 (6 mg:2 mg) Q12 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Choroidal Neovascularization (CNV) Area at Week 12

• 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:
  • REGN910-3 (6 mg:2 mg): mean -3.50 versus -2.20 on control; difference -1.30 (95% CI -3.04 to 0.44), standardized effect d = -0.24; z-test p = 0.143.
  • Aflibercept (IAI) 2 mg: mean -3.70 versus -2.20 on control; difference -1.50 (95% CI -3.21 to 0.21), standardized effect d = -0.25; z-test p = 0.086.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between REGN910-3 (6 mg:2 mg) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept (IAI) 2 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the assessment beyond visual acuity to retinal structure. The registry lists change in central sub-field retinal thickness at Week 12 and Week 36, choroidal neovascularization area at Week 12 and Week 36, and total lesion area at Week 12 and Week 36. Detailed posted summary results are available for central sub-field retinal thickness at both listed times and for choroidal neovascularization area at Week 12. Detailed results for the other listed secondary outcomes are not reported in the registry record.

Across the available secondary summaries, group means show changes from baseline, but the unadjusted comparisons have uncertainty that includes no difference. Variation in these continuous measures is substantial, and the Week 36 treatment sequences differ after the Week 12 re-randomization. These features make the secondary findings useful context rather than a simple confirmation of one primary comparison. The secondary measures assess anatomy, whereas the primary outcome assesses visual function; their results need not be identical or interchangeable.

The secondary analyses should carry less weight than the primary endpoint when forming an overall interpretation. Multiple outcomes, time points, and treatment comparisons create more opportunities for apparently notable findings to arise by chance if many tests are considered without adjustment. The registry record does not report whether a multiplicity procedure was used for the secondary analyses. Their results are therefore best treated as supportive and exploratory unless the prespecified analysis plan indicates otherwise. They do not resolve the uncertainty in the primary visual-acuity comparison.

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

• Change From Baseline in Central Sub-field Retinal Thickness (CST) Measured by Spectral Domain Optical Coherence Tomography (SD-OCT) at Week 12
• Change From Baseline in Central Sub-field Retinal Thickness (CST) Measured by Spectral Domain Optical Coherence Tomography (SD-OCT) at Week 36
• Change From Baseline in Choroidal Neovascularization (CNV) Area at Week 12
• Change From Baseline in Choroidal Neovascularization (CNV) Area at Week 36
• Change From Baseline in Total Lesion Area at Week 12
• Change From Baseline in Total Lesion Area at Week 36

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a numerical change score, and the registry reports a mean and standard deviation for each group. A mean difference compares the average score in one group with the average score in another. A difference near zero indicates similar observed averages, but uncertainty around the estimate must also be considered. An unadjusted recalculation based on group summaries is useful for orientation; it does not reproduce an analysis that adjusts for baseline or other covariates.

What does the confidence interval express?

A confidence interval describes the range of effect values reasonably compatible with the observed data under the statistical model used to construct it. A narrower interval indicates greater precision; a wider interval indicates less precision. When an interval for a difference includes zero, the data do not clearly distinguish a positive difference from no difference or a negative difference at the interval’s stated confidence level. This does not prove the true effect is zero. The interval also needs to be interpreted against a clinically meaningful difference, and such a threshold is not reported in the registry record.

Why are the registry and recalculated estimates different?

The sponsor’s reported comparisons use ANCOVA and are presented as least square mean differences. ANCOVA adjusts a comparison for covariates specified in the analysis. The registry record’s recalculated comparisons instead use posted means, standard deviations, and group sizes to make simple unadjusted estimates. They answer a related but not identical statistical question, so estimates, confidence limits, and p-values can differ. No discrepancy is flagged in the record, but the sponsor’s reported analysis remains the relevant adjusted result.

What does the p-value tell the reader?

A p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It is not the probability that the null hypothesis is true, and it does not quantify the probability that a result is clinically important. A larger p-value is not evidence that two treatments are the same. The primary endpoint’s reported p-values should be read alongside the effect estimates and confidence intervals, not as stand-alone conclusions.

Why does variation matter?

The standard deviation describes how spread out individual change scores are around the group mean. When participant outcomes vary widely, a group mean can be estimated less precisely unless the study has enough information to offset that variation. The primary endpoint standard deviations are sizable relative to the small observed differences between group means. This helps explain why the comparisons remain uncertain despite the reported group sizes.

What is the role of the analysis population?

The registry defines the primary full analysis set using randomization, receipt of any study drug, a baseline measurement, and at least one post-baseline measurement. It also states that LOCF was used for missing BCVA data. LOCF carries the last observed value forward to fill a missing later measurement. In general, this method can be sensitive to assumptions about how outcomes change after the last observation; the registry record does not report enough detail to assess those assumptions or the amount and pattern of missingness.

The registry labels the sponsor comparisons as superiority analyses. The record does not report the full prespecified statistical plan, including whether or how multiplicity was handled across doses, endpoints, and time points. Accordingly, the posted analyses support an interpretation of the reported comparisons, but the available information does not establish how every analysis decision was planned in advance.

11. Confidence Intervals and Precision

The primary endpoint’s sponsor-reported confidence intervals are central to judging precision. For REGN910-3 3 mg:2 mg compared with IAI, the estimated least square mean difference was 0.02 letters, and the 95% confidence interval ranged from -2.99 to 3.03. For REGN910-3 6 mg:2 mg compared with IAI, the estimate was 0.25 letters, and the 95% confidence interval ranged from -2.09 to 2.59. Both intervals include zero, so neither estimate rules out no difference at the stated confidence level.

The intervals also include differences in both directions. That means the data are compatible with some advantage for either group, as well as little or no difference. The central estimates are close to zero, but a small estimate alone is not evidence of equivalence: the interval’s full range matters. The registry record does not provide a clinical threshold for interpreting how large a difference in ETDRS letters would matter.

The unadjusted recalculations have a similar broad pattern of uncertainty. Their intervals are derived from summary statistics and are not substitutes for the sponsor’s adjusted ANCOVA intervals. Both kinds of estimates should be interpreted with attention to the analysis method. The registry does not report an equivalence or non-inferiority margin, so the confidence intervals cannot be used to claim that the treatments met such a criterion.

Precision is also limited by variation in the measured changes and by the available analysis sizes. The posted group standard deviations indicate spread in participant outcomes, while the intervals convey uncertainty in the group comparisons. Neither a confidence interval nor a p-value describes individual outcomes, and these aggregate results cannot establish how a particular participant’s score changed.

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 illustrations translate an observed group difference and its variability into planning examples. All figures in this analysis are participants per arm, not total events. The registry’s own original design assumptions for sample size are not reported in the registry record. The illustrations instead use the observed effect and state a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% probability of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column makes the corresponding illustration for a higher probability of detection. These are planning probabilities under assumptions, not guarantees about a future study. The figures are not observed power.

Rows planning for 100%, 75%, and 50% of the observed effect ask how the illustration changes if the target difference is smaller than, or equal to, the observed difference. Smaller effects are harder to distinguish from background variation, so the planning examples require more participants per arm. The observed effect in a completed study is itself uncertain; treating it as the target for a new study can produce unstable planning figures, especially when the observed difference is small.

The curve should be read in the same planning context: it expresses how the illustrative sample requirement changes with the effect being targeted, rather than reporting observed enrollment or proof that the completed study had a particular probability of success. These figures do not replace a prospective sample-size justification based on a clinically meaningful target, design assumptions, and the planned analysis.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.400; pooled standard deviation σ = 10.564.
2. n = 2 × (1.96 + 0.842)² × 10.564² / 0.400² = 10,949.3, rounded up to 10,950 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.399999999999999                      # observed difference in means
sigma <- 10.5641445597516                     # 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(2713204)
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 = 10,950 (80% power), 14,659 (90% power)
 75% of observed effect: n per arm = 19,466 (80% power), 26,059 (90% power)
 50% of observed effect: n per arm = 43,798 (80% power), 58,633 (90% power)
power.t.test: 10950.3 
Simulated power at n = 10,950 per arm: 0.797 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons using ANCOVA and least square mean differences. For the 3 mg:2 mg REGN910-3 group versus IAI, the reported estimate was 0.02 letters, with a 95% confidence interval from -2.99 to 3.03 and p = 0.989. For the 6 mg:2 mg group versus IAI, the reported estimate was 0.25 letters, with a 95% confidence interval from -2.09 to 2.59 and p = 0.835. These are adjusted analyses, not direct subtractions of the posted group means.

The recalculations are unadjusted comparisons based on the posted summary statistics. They give estimates that are close to zero, with confidence intervals that also include no difference. Small differences between recalculated values and sponsor estimates are expected because ANCOVA and unadjusted mean comparisons need not produce the same estimate or uncertainty. The registry does not flag a discrepancy. The sponsor’s own analysis is the appropriate reference for the reported adjusted comparison; the recalculation provides a separate, transparent summary-statistic check rather than a replacement.

The registry record does not report the full ANCOVA specification, including all covariates and detailed model diagnostics. As a result, the reported estimates can be described, but the adjusted model cannot be independently reconstructed from the record alone.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several hypotheses, such as multiple doses, endpoints, or follow-up times. If each test is interpreted without adjustment, the chance of at least one apparently positive result can increase across the collection of tests. A prespecified hierarchy or multiplicity adjustment can help control that risk, but the registry record does not report whether either approach was used for the primary and secondary comparisons.

The posted outcomes include a primary visual-acuity endpoint and multiple secondary anatomical measures at different times. The analysis record also contains multiple reported analyses. The registry record does not report a complete statistical analysis plan identifying which comparisons were confirmatory, how the testing order was set, or how multiplicity was handled. It is therefore not possible to determine from the record whether a particular p-value was adjusted for the other tests.

Missing-data handling is described for the primary endpoint: last observation carried forward was used, and the full analysis set required a baseline measurement and at least one post-baseline assessment after study drug receipt. However, the amount and pattern of missing data, reasons for missingness, and sensitivity analyses under alternative assumptions are not reported in the registry record. LOCF is a method of imputation, not a guarantee that missing outcomes are unbiasedly represented.

The record does not report the full analysis population definitions for every secondary outcome or detailed handling of missing measurements for those outcomes. Nor does it report the full model specification for the sponsor’s ANCOVA analyses. These gaps limit independent assessment of how analysis choices may affect the estimates. They do not invalidate the posted results, but they constrain how confidently readers can assess robustness and confirmatory status.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (5.0%), cellulitis (3.3%), cardiac failure congestive (1.7%), pericardial effusion (1.7%), diverticulitis intestinal haemorrhagic (1.7%).

The registry reports serious adverse events and other adverse events by group, along with deaths. For the REGN910-3 3 mg:2 mg group, the serious adverse event figures were 11 affected among 60 at risk, and the other adverse event figures were 17 among 60 at risk; 1 death was reported. For the REGN910-3 6 mg:2 mg group, the corresponding figures were 20 among 122 and 41 among 122, with 2 deaths. For IAI 2 mg, they were 30 among 183 and 51 among 183, with 7 deaths. A further group labelled IAI 2mg to REGN910-3 had 8 among 58 serious adverse events, 20 among 58 other adverse events, and 3 deaths.

These are descriptive registry counts, not adjusted comparisons of safety risk. The group labelled IAI 2mg to REGN910-3 reflects a treatment sequence, so it should not be read as an unchanged initial-treatment group. The registry lists pneumonia at 5.0%, cellulitis at 3.3%, and cardiac failure congestive, pericardial effusion, diverticulitis intestinal haemorrhagic, and staphylococcal infection at 1.7% each among the leading serious event terms. The record does not establish that a treatment caused any particular event, and these figures alone are not a complete safety assessment.

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

The Week 12 primary results describe average changes in ETDRS letters and adjusted comparisons between study groups. The reported least square mean differences are close to zero, and their 95% confidence intervals include no difference. The findings therefore do not provide a clear statistical distinction between the groups on this endpoint at this time point. They also do not establish that the treatments are equivalent or that their effects are identical.

A non-significant test does not prove absence of an effect. The confidence intervals retain values in both directions, and the registry record does not provide a prespecified clinical margin for deciding which differences would be important. A claim of equivalence or non-inferiority would need a suitable design, margin, and analysis; those details are not reported in the registry record.

The endpoint is a measure of visual function, and its group mean does not indicate that all participants had the same response. The registry used LOCF for missing BCVA measurements. Without reported detail on missingness and sensitivity analyses, readers cannot determine how much the missing-data method influences the result.

The anatomical secondary outcomes add context, but they are not substitutes for BCVA and should be interpreted cautiously given multiple comparisons and incomplete reporting of the analysis plan. Safety counts are also descriptive and do not establish causation. Overall, the registry supports a measured account of the observed outcomes and their uncertainty; it does not justify broader conclusions beyond the comparisons, endpoints, and follow-up reported.

18. Why This Trial Matters Statistically

This trial illustrates why interpreting a clinical comparison requires more than reading the group averages or a p-value. The observed Week 12 mean changes are close across groups, but the meaningful statistical question is how precisely the between-group contrasts are estimated. The sponsor-reported confidence intervals show that a range of positive and negative differences remains compatible with the data.

It also demonstrates the distinction between an adjusted sponsor analysis and an unadjusted recalculation from summary statistics. The former uses ANCOVA and reports least square mean differences; the latter is a transparent comparison of posted means and standard deviations. They are related, but not interchangeable. Keeping that distinction clear prevents an unadjusted check from being mistaken for the trial’s primary analysis.

The study’s changing treatment schedules after Week 12 are important for later outcomes. Week 36 comparisons concern different treatment sequences following re-randomization, so they cannot be read as if all groups remained on their original schedules. The results also show why secondary outcomes and safety summaries need their own cautious interpretation, especially when the record does not explain multiplicity handling or fully report analysis details.

Finally, planning illustrations based on observed effects do not reveal the completed study’s power or its original design rationale. Separating planning calculations from observed evidence, and estimates from certainty, is central to sound biostatistical reading.

19. Limitations

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

The registry record leaves several details unavailable for independent evaluation. It does not report the original sample-size justification, the full statistical analysis plan, the complete ANCOVA specification, or whether multiplicity adjustments were used. The planning illustrations are derived from observed effects and are not evidence of the study’s original design assumptions.

The primary endpoint uses LOCF for missing data, but the record does not provide the extent or pattern of missingness, reasons for missing assessments, or sensitivity analyses using alternative assumptions. The analysis population is defined, yet the record does not provide enough detail to assess how the missing-data approach may have influenced the group comparisons.

The posted endpoint results are aggregate summaries. They do not show participant-level distributions or allow assessment of whether a mean adequately represents the range of responses. The primary adjusted comparisons are reported, but the model details needed to reproduce them are not available in the registry record. The recalculated comparisons are therefore necessarily unadjusted.

Some secondary outcomes are listed without detailed summary results in the registry record. Secondary measures also involve multiple time points and comparisons, while multiplicity handling is not reported. In addition, Week 36 groups follow different schedules after re-randomization, complicating simple comparisons with the original groups. Finally, adverse event counts are descriptive, include different treatment sequences, and do not establish causation. These limitations call for restrained interpretation rather than conclusions beyond the posted comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Anti-angiOpoeitin 2 Plus Anti-vascular eNdothelial Growth Factor as a therapY for Neovascular Age Related Macular Degeneration: Evaluation of a fiXed Combination Intravitreal Injection — NCT02713204.
• Registry record last updated 2019-05-07; status last verified 2019-04.
• Results first posted 2019-05-07.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, quadruple-masked, active-controlled phase 2 study of intravitreal REGN910-3 compared with intravitreal aflibercept in participants with neovascular age-related macular degeneration. Enrollment was 365. The primary endpoint was change from baseline in ETDRS BCVA letters at Week 12, with LOCF used for missing data in the stated full analysis set.

The sponsor’s ANCOVA comparisons of REGN910-3 with IAI produced estimates close to zero, with 95% confidence intervals that included no difference. Unadjusted recalculations from the posted summary statistics show the same broad pattern of uncertainty but are not substitutes for the sponsor analysis. Secondary anatomical outcomes and adverse event counts provide additional descriptive information; multiplicity procedures, the complete analysis plan, and several other design and analysis details are not reported in the registry record.