Study of the Intravitreal Plasma Kallikrein Inhibitor, KVD001, in Subjects With Center-involving Diabetic Macular Edema (ciDME): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of the Intravitreal Plasma Kallikrein Inhibitor, KVD001, in Subjects With Center-involving Diabetic Macular Edema (ciDME) (NCT03466099), a randomized phase 2 study. The primary outcome is BCVA.

2. Clinical Question

3. Trial Design

This was a randomized, sham-controlled, quadruple-masked, parallel-group Phase 2a study of KVD001. The registry lists three groups: high-dose KVD001, low-dose KVD001, and sham procedure. The study condition was diabetic macular edema, specifically center-involving disease in the official title. That title also identifies prior anti-vascular endothelial growth factor treatment as part of the population description.

The brief summary describes four injections into the eye at monthly intervals. It says participants were assigned to high dose, low dose, or sham, and that the study would assess vision and the course of disease in the eye. The arm descriptions themselves do not provide dose amounts or further procedural detail, so those details are not reported in the registry record.

The registry lists enrollment as 129 and marks the study completed. The primary completion date is 2019-10-10, and the start date is 2018-02-16. The posted primary outcome uses group sizes of 40.0 for high dose, 44.0 for low dose, and 44.0 for sham. These outcome-specific group sizes need not describe every participant enrolled, and the registry record does not explain the relationship between enrollment and the outcome denominators.

The principal outcome was change from baseline in best corrected visual acuity at 16 weeks, reported as a mean with standard deviation. The registry also lists DRSS and CST as secondary outcomes; numerical results are posted for CST, while numerical DRSS results are not reported in the registry record. The registry record does not report the original design assumptions used to choose enrollment or the detailed analysis populations.

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: 130 Patients were randomized but one patient withdrew prior to receiving any study treatments

Overall Study

Reasons for not completing this period:

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 BCVA, measured over 16 weeks.

The primary endpoint is change from baseline in best corrected visual acuity (BCVA), measured in letters, at 16 weeks. BCVA assesses visual acuity under standardized correction, so a change score expresses how the measured acuity at the assessment time differs from the participant’s baseline measurement. The registry reports group means and standard deviations, then gives mean differences comparing each KVD001 group with sham.

Using a change score makes the comparison about movement from baseline rather than only the final measured value. A mean summarizes the average change within a group; the standard deviation describes how dispersed individual changes are around that group mean. These summaries answer different questions: the mean indicates the group’s average direction and size of change, while the standard deviation conveys variation among participants.

BCVA is relevant to a study whose stated purpose includes evaluating vision. The registry also describes interest in changes in the underlying eye disease, reflected in secondary outcome listings such as CST and DRSS. The primary endpoint remains the prespecified focus identified by the registry record, but the record does not report the detailed protocol definition, measurement procedures, or analysis population for that endpoint.

A group mean does not describe every participant’s experience, and a between-group mean difference does not establish an individual outcome. Interpretation therefore depends not only on the point estimate but also on its uncertainty, the trial’s analysis methods, and how completely outcomes were observed and reported.

7. Results Posted in the Registry

• KVD001 Injection (High Dose): mean 0.80 versus -1.80 on control; difference 2.60 (95% CI -1.57 to 6.77), standardized effect d = 0.26; z-test p = 0.222.
• KVD001 Injection (Low Dose): mean -0.30 versus -1.80 on control; difference 1.50 (95% CI -2.89 to 5.89), standardized effect d = 0.14; z-test p = 0.503.

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.

CST

• 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:
  • KVD001 Injection (High Dose): mean 10.90 versus 8.20 on control; difference 2.70 (95% CI -46.21 to 51.61), standardized effect d = 0.02; z-test p = 0.914.
  • KVD001 Injection (Low Dose): mean 2.30 versus 8.20 on control; difference -5.90 (95% CI -54.63 to 42.83), standardized effect d = -0.05; z-test p = 0.812.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between KVD001 Injection (High Dose) 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 KVD001 Injection (Low Dose) and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies DRSS and CST as secondary outcomes, but numerical results are posted only for CST. DRSS numerical results are not reported in the registry record, so the secondary outcome record is incomplete for judging whether the anatomical and grading measures align with the visual-acuity result.

For CST, the posted comparison estimates are close to zero relative to their confidence intervals, and both intervals include zero. The unadjusted p values also do not indicate clear separation from sham. Taken as a broad pattern, the posted CST summaries do not offer a precise, independent signal that resolves the uncertainty in the primary BCVA comparisons. They are contextual evidence, not a substitute for the primary outcome.

Secondary endpoints can help describe different dimensions of a condition and may support a coherent interpretation when their results are consistent. They can also produce mixed patterns because they measure different features, have different variability, and may have different amounts of missing information. The registry does not provide enough analysis detail to determine whether all planned secondary measures, time points, or analyses are represented in the posted results.

Unadjusted secondary findings carry less weight when several outcomes or comparisons may be examined. Without a reported multiplicity strategy, an isolated small p value, if present, would need cautious interpretation because repeated testing can increase the chance of a seemingly unusual result. In this record, the numerical CST results do not remove the uncertainty around BCVA, and absent DRSS results cannot be used to support or contradict it.

Overall, the secondary record is most useful as context for the primary comparison, not as a separate basis for a definitive conclusion. The registry reports no secondary analyses in the reported-analyses listing. Details on analysis populations and missing-data handling are not reported in the registry record, which further limits cross-outcome interpretation.

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

• DRSS
• CST

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods help distinguish the observed group summaries from the uncertainty and assumptions behind a comparison. The registry reports means and standard deviations for a continuous primary outcome, estimates of mean differences against sham, confidence intervals, and unadjusted p values. The planning illustrations use the observed effects under stated assumptions; they are not the trial’s original design calculations.

What does a mean difference represent?

A mean difference compares the average change in one group with the average change in another. For the primary endpoint, the comparison is each KVD001 dose group against sham. A positive estimate means the reported group mean change is numerically higher in the KVD001 group than in sham, given the way the comparison is defined. It does not mean every participant changed by that amount, and it does not describe the full distribution of individual outcomes.

The registry reports the group standard deviations as well as the mean changes. Standard deviation describes variation among measurements within a group. It is not the uncertainty interval for the group mean or the between-group difference. The standard error is a measure of uncertainty in an estimate; the registry’s comparison summaries include standard errors for the group means. In general, larger participant-to-participant variation and smaller group sizes tend to make estimates less precise.

How should the confidence intervals be understood?

A confidence interval expresses the statistical uncertainty around an estimated difference under the method used to construct it. It provides a range of values compatible with the observed data and model assumptions, rather than a guarantee that the true difference lies in that particular interval. An interval spanning zero means the data do not clearly distinguish a positive difference from no difference or a negative difference at the stated confidence level. It does not prove that the groups are equivalent.

For the BCVA comparisons, both intervals span zero. That pattern accords with the unadjusted p values reported in the registry. The p value is calculated under a null hypothesis and test assumptions; it describes how unusual data at least as incompatible with that hypothesis would be under those conditions. It is not the chance that the null hypothesis is true, nor a measure of clinical importance. Because the posted p values are unadjusted, they do not account for testing multiple outcomes or comparisons.

What does the standardized effect describe?

The comparison summaries also report a standardized effect, which expresses the estimated mean difference relative to a pooled standard deviation. This places an estimate on a scale that is less tied to the original measurement units. Standardization can assist comparisons across outcomes, but it does not replace the original-unit estimate or its confidence interval. The standardized value inherits the limitations of the observed data and should not be interpreted as a direct measure of patient importance.

The registry reports pooled standard deviations for the BCVA and CST comparisons. Those values support the displayed standardized effects. They are not additional outcome changes, and they do not resolve uncertainty in the estimated mean differences. The estimates are based on observed group summaries; the registry does not report adjusted model results.

Why do analysis details matter?

Randomization is intended to support a fair comparison by assigning participants to groups by chance, while masking can reduce the influence of knowledge of assignment on care, assessment, or reporting. The record identifies randomized allocation and quadruple masking. It does not report the specific roles masked, how masking was maintained, or whether any participants or investigators became unmasked.

Analysis populations and missing-data methods can affect a result, especially when the measured outcome is unavailable for some participants. The primary endpoint population is not specified in the registry record, and missing-data handling is not reported in the registry record. The record also does not report the model used for the primary comparison, covariate adjustments, or checks of model assumptions. Consequently, the posted summaries can be described, but their exact analytical construction cannot be fully reconstructed from the registry record.

Multiplicity is another consideration. When several doses, outcomes, or time points are assessed, the chance of at least one apparently unusual result can increase if each test is interpreted separately. The registry posts unadjusted comparisons and lists secondary outcomes, but a strategy for controlling multiplicity is not reported in the registry record. This is why the primary outcome and secondary outcomes should not be treated as if each were a separate confirmatory test.

What is the role of the planning illustrations?

The planning illustrations recalculate sample-size requirements from the observed effect under stated assumptions. They are not observed power and do not describe the trial’s own sample-size justification. Their role is to show how required group size changes under hypothetical future planning assumptions, including smaller target effects. Because the observed effects are uncertain, sample-size calculations based on them are also uncertain and should not be treated as a definitive design recommendation.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an estimated group difference. The BCVA point estimates are 2.6 letters for high dose versus sham and 1.5 letters for low dose versus sham. Their confidence intervals, from -1.57 to 6.77 and from -2.887 to 5.887, respectively, are broad and each crosses zero. The estimates therefore do not pin down a single direction or magnitude with high precision.

For high dose, the interval includes values below zero as well as values above the point estimate. For low dose, the interval likewise ranges from a negative difference to a positive difference. The values at the ends of an interval are not equally likely descriptions of the true effect, and the interval is not a range containing every participant’s outcome. It conveys uncertainty about the estimated group contrast.

Group variability is also relevant. The BCVA standard deviations were 6.65 in the high-dose group, 8.36 in the low-dose group, and 12.27 in the sham group. Variation within groups is distinct from uncertainty in the comparison, but it contributes to how precisely a mean contrast can be estimated alongside the group sizes. The registry reports outcome group sizes of 40.0, 44.0, and 44.0, respectively.

These confidence intervals are unadjusted comparison intervals as posted. The registry record does not report whether or how the intervals account for multiple comparisons, missing outcomes, or covariate adjustment. Their interpretation should therefore remain tied to the reported summaries and not be extended to unreported analyses or populations.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total event counts. The outcomes are continuous, so the figures describe the number of participants in each of two equally allocated comparison arms under the planning calculation. The total-event convention applies to time-to-event calculations, not these figures.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect: 100%, 75%, or 50%. These are planning illustrations calculated from the observed comparisons, not the original study’s design assumptions; those original assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical design with an 80% chance of detecting the specified effect under those assumptions, if that effect is the true effect and the calculation model applies. The 90% power column expresses the corresponding planning target at 90% power. These percentages describe prospective design properties under assumptions; they do not express the probability that a result in this completed trial is correct.

For each comparison, the planning figures rise as the target effect is reduced from the full observed effect to a smaller fraction. This is the expected relationship: a smaller difference is harder to distinguish from random variation, so more participants are needed to reach the same planned power. Because the observed effects themselves have uncertainty, the illustrations should be read as conditional scenarios rather than precise prescriptions. This is not observed power.

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 = 2.600; pooled standard deviation σ = 9.999.
2. n = 2 × (1.96 + 0.842)² × 9.999² / 2.600² = 232.2, rounded up to 233 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 <- 2.6                      # observed difference in means
sigma <- 9.99905617497191                     # 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(3466099)
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 = 233 (80% power), 311 (90% power)
 75% of observed effect: n per arm = 413 (80% power), 553 (90% power)
 50% of observed effect: n per arm = 929 (80% power), 1,244 (90% power)
power.t.test: 233.1 
Simulated power at n = 233 per arm: 0.803 (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

Multiplicity arises when a study assesses several outcomes, doses, time points, or statistical comparisons. If each is evaluated separately without adjustment, the chance of at least one apparently unusual result can be higher than for a single planned test. That does not make an individual result false, but it changes how persuasive an isolated p value is. The registry posts unadjusted p values for the primary comparisons and does not report a multiplicity procedure in the registry record.

The record identifies a primary outcome and lists DRSS and CST as secondary outcomes. Numerical CST summaries are present, while numerical DRSS results are not reported in the registry record. The registry lists zero reported analyses. This does not establish that no analyses were performed; it means that analysis details and results beyond those posted cannot be assessed from the registry record. The original statistical analysis plan, including any hierarchy or adjustment approach, is not reported in the registry record.

Missing data are important because the estimated group means depend on which participants contributed outcome measurements and how unavailable measurements were handled. The registry does not report the primary analysis population, the number with missing primary outcome data, reasons for missingness, or a method for handling missing values. It is therefore not possible to assess from the posted record whether missingness differed by group or how alternative methods might affect the results.

The record also does not report whether the primary analysis followed an intention-to-treat principle, a per-protocol approach, or another population definition. Randomized allocation supports comparison at assignment, but interpretation of the reported outcome requires knowing which participants were included and how deviations from assigned treatment were handled. These details are not reported in the registry record.

Without a reported multiplicity strategy, analysis population, or missing-data method, the estimates remain interpretable as posted descriptive and unadjusted comparisons, but their inferential context is incomplete. These reporting gaps are limitations in what can be concluded from the registry record; they do not justify guessing which methods were used.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angina pectoris (4.5%), abdominal pain (2.4%), chronic hepatic failure (2.4%), staphylococcal infection (2.4%), fall (2.4%).

The registry reports serious adverse events for each group as affected participants and participants at risk: high dose, 3 of 41; low dose, 3 of 44; and sham, 2 of 44. Deaths are reported as 0 in each group. These are descriptive counts, not estimates of whether KVD001 caused an event or whether the groups differ reliably in risk.

The registry also lists serious adverse-event terms, including angina pectoris at 4.5%, and abdominal pain, chronic hepatic failure, staphylococcal infection, fall, and hypoglycaemia at 2.4% each. The listed terms do not by themselves establish causation, severity beyond the registry’s serious-event classification, or a comparative risk. The record does not provide enough detail to determine how terms were distributed across groups or whether events were judged related to study treatment.

Other adverse events are reported separately: 22 of 41 in high dose, 26 of 44 in low dose, and 23 of 44 in sham. Serious and other adverse-event categories should not be conflated. These summaries describe what the registry reports; assessment of safety also depends on event definitions, follow-up, exposure, and attribution methods, which are not fully reported in the registry record.

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

The posted primary results describe mean BCVA change at 16 weeks and estimated differences between each KVD001 dose group and sham. The estimates are positive relative to sham, but their confidence intervals include zero and the unadjusted p values do not provide clear statistical evidence of a group difference. The data therefore leave substantial uncertainty about the magnitude and direction of the underlying differences.

That interpretation is not equivalent to demonstrating that the groups are the same. A failure to establish a difference does not establish equivalence, and no equivalence margin or non-inferiority framework is reported in the registry record. The posted comparisons also do not establish that any observed average applies to every participant. Group means describe averages, while individual outcomes can vary.

Nor do these results alone establish effects beyond the measured outcome and assessment time. The primary endpoint is BCVA change at 16 weeks; the registry lists secondary outcomes concerning DRSS and CST, but numerical DRSS results are not reported. The record does not support extending the findings to other durations, populations, treatment schedules, or clinical decisions.

The study is identified as randomized, sham-controlled, quadruple-masked, parallel-group, and Phase 2a. Those features describe the trial structure but do not eliminate uncertainty from limited group sizes, outcome variability, missing-data handling, or incomplete reporting of analysis methods. The registry does not report the original sample-size justification, the analysis populations, or the approach to multiplicity.

Safety counts likewise describe reported events without establishing causation or comparative risk. The registry reports zero deaths in each group and serious adverse-event counts, but the record does not provide a complete causal assessment. Overall, the posted results are best read as estimates from this trial with meaningful uncertainty and reporting limitations, rather than as a definitive statement about treatment benefit or harm.

17. Why This Trial Matters Statistically

This trial is statistically informative because it includes both KVD001 dose groups and a sham comparator, with randomized allocation and masking reported in the registry. A sham-controlled comparison helps distinguish outcomes observed after the intervention from changes that may occur under the study procedure and follow-up context. Randomization is intended to reduce systematic differences between groups, while masking is intended to limit influences from awareness of assignment.

The primary endpoint is a continuous change measure, and the registry gives group means, standard deviations, mean differences, confidence intervals, and unadjusted p values. Together, these summaries let readers see both the estimated direction and the uncertainty, rather than relying on a point estimate alone. In this case, the intervals crossing zero make precision central to interpretation.

The presence of more than one dose and secondary outcomes also illustrates why a trial’s analysis plan matters. Multiple comparisons can complicate interpretation, particularly when the registry does not report whether a multiplicity procedure was planned. Similarly, missing-data and analysis-population details are needed to understand exactly which observations support the results.

The planning illustrations show how sample-size requirements depend on the effect a future study aims to detect. A smaller target effect requires more participants under the stated assumptions. This is useful for understanding design trade-offs, while keeping clear that those calculations are not the original trial’s justification and do not reveal the power of the completed study.

More broadly, this record demonstrates the value of separating observed estimates from certainty, distinguishing primary from secondary outcomes, and treating registry summaries as a basis for careful statistical reading rather than a complete substitute for detailed methods and results reporting.

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 primary comparisons are based on relatively small posted outcome groups, and the standard deviations indicate variation in BCVA change. The resulting confidence intervals are wide and include zero. This limits precision, regardless of the direction of the point estimates. The registry does not report the original sample-size justification, so it is not possible to judge the planned detectable effect or whether the enrollment target was chosen for the primary endpoint.

Outcome denominators are not identical across the posted BCVA groups, and the registry does not explain the difference between total enrollment and the outcome-specific group sizes. The analysis population, missing outcome counts, reasons for missingness, and methods for handling missing data are not reported in the registry record. These omissions limit assessment of whether the posted comparisons could be affected by incomplete follow-up.

Some endpoint reporting is incomplete. DRSS is listed as a secondary outcome, but numerical DRSS results are not reported in the registry record. The record also does not report a multiplicity strategy, detailed statistical model, covariate adjustment, or the original analysis plan. The p values are explicitly unadjusted, so their interpretation does not account for any unreported family of tests.

The arm descriptions do not specify dose amounts, and the registry does not provide detailed information on masking roles or treatment adherence. Safety summaries provide counts but limited detail about timing, attribution, and group distribution of individual serious-event terms. These limitations are specific to the information available in this registry record and should not be mistaken for evidence that the unreported procedures were or were not performed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of the Intravitreal Plasma Kallikrein Inhibitor, KVD001, in Subjects With Center-involving Diabetic Macular Edema (ciDME) — NCT03466099.
• Registry record last updated 2021-01-28; status last verified 2021-01.
• Results first posted 2020-12-08.
• 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

The registry record describes NCT03466099, a completed randomized, sham-controlled, quadruple-masked, parallel-group Phase 2a study sponsored by KalVista Pharmaceuticals, Ltd. The study evaluated intravitreal KVD001 in people with center-involving diabetic macular edema who had prior anti-vascular endothelial growth factor treatment. The primary outcome was change from baseline in BCVA at 16 weeks.

The posted mean differences versus sham were 2.6 letters for high dose and 1.5 letters for low dose. Both confidence intervals include zero, and the unadjusted p values are 0.222 and 0.503. Numerical CST results are posted; numerical DRSS results are not reported in the registry record. The record reports serious adverse-event counts and no deaths in the listed groups.

Important details, including missing-data handling, analysis populations, multiplicity methods, and the original sample-size justification, are not reported in the registry record. The results should therefore be read as uncertain registry-posted comparisons rather than definitive conclusions.