Safety and Efficacy Study for the Treatment of Painful Diabetic Neuropathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study for the Treatment of Painful Diabetic Neuropathy (NCT01475786), a randomized phase 2 study. The primary outcome is The Primary Study Endpoint Was the Change in Average 24-hour Pain Score From Baseline to the 6-month Follow-up..

2. Clinical Question

3. Trial Design

The registry describes a Phase II, randomized, double-blind, placebo-controlled, multicenter study. It used a parallel-group design and lists enrollment of 104. The condition was painful diabetic neuropathy, and the study status is completed. The record lists a start date of 2012-08 and a primary completion date of 2014-03-12.

Participants were assigned to a low-dose Engensis (VM202) group, a high-dose Engensis (VM202) group, or a normal-saline placebo group. The intervention descriptions identify 16 mg and 32 mg Engensis doses. The low-dose arm title includes both Engensis and placebo, and its description says saline injections were also given. The placebo arm is described as receiving normal saline. Allocation concealment details and the roles of people who were masked are not reported in the registry record.

The primary outcome is continuous: change in average 24-hour pain score from baseline. However, the record does not give a consistent follow-up description. The outcome title refers to change through the 6-month follow-up, while its timeframe says the seven days before the 9 Month visit. The outcome description says the diary was completed before the 6 month follow-up. These descriptions cannot be reconciled from the registry record.

The endpoint population is defined by receipt of the correct assigned dose on both dosing days, having the Day 180 assessment, and having no protocol violations or major deviations. The number randomized to each arm and the reasons for exclusion from this efficacy population are not reported in the registry record. Original sample-size justification and the trial's own statistical analysis plan are also not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Efficacy population included all subjects who received the correct dose of study drug based on the randomization schedule at both Days 0 and 14, have the Day 180 assessment, and did not have any protocol violations or major deviations

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Subjects in the intent to treat (ITT) population were those who were randomized and received study treatments

6. Primary Endpoint

The registry lists the primary outcome as The Primary Study Endpoint Was the Change in Average 24-hour Pain Score From Baseline to the 6-month Follow-up., measured over seven (7) days before 9 Month visit.

The primary endpoint is the change in the average 24-hour pain score from baseline. The diary asked participants to rate daily pain intensity on an 11-point numerical scale, where 0 means no pain and 10 means worst possible pain. The average was based on daily entries over seven days before the relevant assessment period. The registry says the baseline diary was completed during screening before the first injections, with another diary before follow-up.

Change scores are used to describe how an outcome differs from its starting value. A negative posted mean change indicates a lower average score at follow-up than at baseline; it is a numerical description, not by itself evidence that the intervention caused the change. Comparing changes between groups is intended to account for each group's starting score while assessing whether their observed trajectories differ.

The registry's timing descriptions are inconsistent: the endpoint title identifies the 6-month follow-up, the timeframe refers to the seven days before the 9 Month visit, and the description refers to the 6 month follow-up. The precise intended measurement visit is therefore not reported consistently in the registry record. The record also does not report an endpoint confidence level or a posted sponsor analysis for this outcome.

7. Results Posted in the Registry

• High Dose 32mg Engensis (VM202): mean -1.94 versus -2.78 on control; difference 0.84 (95% CI -0.17 to 1.85), standardized effect d = 0.40; z-test p = 0.104.
• Control - Placebo (Normal Saline): mean -1.59 versus -2.78 on control; difference 1.19 (95% CI -0.00 to 2.38), standardized effect d = 0.56; z-test p = 0.051.

8. Statistical Interpretation

9. Statistical Methods Explained

The outcome is a continuous measure: an average pain score recorded on a numerical rating scale. For continuous outcomes, a group mean describes the central value of the observations, while a standard deviation describes how spread out individual observations are around that mean. A standard deviation is not a confidence interval and does not directly express uncertainty in the group mean.

What does a change score mean?

Each participant's change score is based on a follow-up value relative to baseline. The reported arm means are averages of these changes for the efficacy population. A negative average change means the follow-up scores were lower than baseline on the scale; it does not identify the reason for the change. The placebo group also has a negative mean change, illustrating why within-group change alone cannot distinguish intervention effects from other explanations, such as changes that occur over time or measurement variation. This is a general statistical point, not a claim about what caused the observed changes in this trial.

How should the mean differences be read?

The posted recalculated comparisons express the difference between an arm's mean change and the low-dose Engensis-and-placebo group's mean change. Under that comparison convention, a positive value means the compared arm's mean change is numerically higher, or less negative, than the reference mean change. These are simple, unadjusted comparisons of posted summary statistics. They are not adjusted estimates from a model that accounts for baseline characteristics or other covariates. The registry record does not report an adjusted analysis.

The recalculated standard errors and pooled standard deviations are calculation details for these unadjusted comparisons. They do not replace the original trial's analysis, and the registry record does not include a sponsor analysis for these comparisons. The record's discrepancy indicator is false, so there is no flagged discrepancy between the posted summaries and these calculations. Nonetheless, the registry does not state a trial-specific model or analysis procedure that would establish whether these simple comparisons match the intended primary analysis.

What do p-values contribute?

A p-value describes how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The values posted for these comparisons are unadjusted. The record does not report whether the trial's own analysis used a different test, adjusted for multiple comparisons, or included covariates. Accordingly, the recalculated p-values should be read as descriptive inferential calculations, not as a substitute for an unreported sponsor analysis.

Why does spread matter?

Participants' pain scores can vary, and the standard deviations describe observed variability in the change scores. Greater variability generally makes a group mean harder to estimate precisely when other features are held constant. The comparison calculations use pooled standard deviations, a way of combining within-group spread under assumptions about variability. That method is a general statistical approach; the registry does not report a trial-specific justification for its use. The posted group standard deviations are not identical, which is another reason not to assume that a simplified calculation fully represents the trial's planned analysis.

General statistical methods can also account for repeated measurements, baseline scores, site, or other prespecified factors, but the registry record does not report that such methods were used. It does not report the original analysis plan, the primary test, handling of protocol deviations beyond the efficacy-population definition, or checks of model assumptions. Those details should not be inferred from the presence of group means and standard deviations.

Who contributes to the endpoint summaries?

The registry defines the efficacy population as subjects who received the correct randomized dose at both Days 0 and 14, had the Day 180 assessment, and did not have protocol violations or major deviations. That definition describes a selected analysis population. It does not state how many randomized participants were excluded under each criterion, or whether outcome data for excluded participants were examined in another analysis. The record lists no posted secondary outcomes and no posted analyses beyond the primary outcome summary.

Missing-data methods matter because participants without follow-up scores may differ from those with observed scores. General approaches can include model-based methods, imputation, or sensitivity analyses, but which approach was used is not reported in the registry record. The same applies to any interim analysis or stopping rule: the record does not report these details, and they should not be guessed.

Finally, the primary outcome timing is not consistent across its title, timeframe, and description. Statistical interpretation depends on knowing which visit and diary period the endpoint represents. The registry record does not resolve that discrepancy. The posted numbers can still be described as the reported group summaries and recalculated contrasts, but their exact relationship to the intended endpoint visit remains unclear.

10. Confidence Intervals and Precision

A confidence interval gives a range of values that are reasonably compatible with the data under the calculation method. It communicates precision as well as direction: a narrower interval indicates a more precise estimate than a wider interval, all else being equal. The confidence level used for the posted recalculated intervals is not reported in the registry record, so it should not be assumed from the intervals alone.

For high dose compared with the low-dose Engensis-and-placebo reference, the recalculated mean difference is 0.84, with an interval from -0.173 to 1.853. This range includes zero and extends to values on both sides of it. The interval therefore reflects uncertainty about both the direction and magnitude of the contrast.

For placebo compared with the same reference, the recalculated mean difference is 1.19, with an interval from -0.003 to 2.383. Its lower limit is slightly below zero, so this interval also includes zero. The estimates are not precise enough to rule out a zero difference under the calculation used. The interval limits should not be interpreted as a range of individual participant changes.

These are unadjusted recalculations from posted summary statistics, not intervals reported from a sponsor analysis. They do not account for any unreported covariate adjustment or multiplicity procedure. The group standard deviations describe the spread of participant-level changes; they are distinct from the uncertainty intervals for between-group mean differences. The endpoint timing inconsistency and the selected efficacy population also affect how confidently these estimates can be generalized to the trial's intended comparison.

11. 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. They are illustrations calculated from the observed effect, not the trial's original design justification. The registry record does not report the trial's own sample-size assumptions or justification. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect.

The 80% power column describes a planning scenario that would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column describes the corresponding scenario with a higher planned chance of detection. These are design calculations, not statements about the chance that the observed result is real or that a treatment works. This is not observed power.

Rows planning for 75% or 50% of the observed effect require more participants per arm than planning for the full observed effect. Smaller effects are harder to distinguish from random variation, so more participants are generally needed to achieve the same planned power under otherwise comparable assumptions. The estimates are specific to the observed effects used in the recalculations and the stated simplified assumptions. They are not a replacement for a trial-specific design analysis, and the registry record does not report the assumptions used when the original study was planned.

12. 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 = 0.840; pooled standard deviation σ = 2.089.
2. n = 2 × (1.96 + 0.842)² × 2.089² / 0.840² = 97.1, rounded up to 98 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 <- 0.84                      # observed difference in means
sigma <- 2.08895630915021                     # 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(1475786)
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 = 98 (80% power), 130 (90% power)
 75% of observed effect: n per arm = 173 (80% power), 232 (90% power)
 50% of observed effect: n per arm = 389 (80% power), 520 (90% power)
power.t.test: 98.1 
Simulated power at n = 98 per arm: 0.800 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record lists one posted outcome measure and no posted secondary outcomes. It also lists no posted analyses. The posted comparisons include high dose versus the low-dose Engensis-and-placebo reference and placebo versus that reference. The record does not explain whether these comparisons were prespecified, whether additional analyses were conducted, or whether any multiplicity adjustment was planned or applied.

Multiplicity is the issue that arises when several hypotheses or outcomes are tested: the chance of obtaining at least one apparently unusual result can increase as the number of tests grows. This is a general statistical consideration. Because the registry does not report the full analysis plan or multiplicity handling, the unadjusted p-values should not be treated as if they necessarily reflect a single, prespecified test.

Missing-data handling is also not reported in the registry record. The primary endpoint's stated efficacy population required a Day 180 assessment and excluded subjects with protocol violations or major deviations. The record does not describe how many participants lacked endpoint data, how exclusions were applied, or whether sensitivity analyses assessed the effect of missing observations. It does not report whether an intention-to-treat population was analyzed.

The difference between the enrollment figure and the endpoint arm counts should not be interpreted as a complete account of attrition: the record does not provide a participant flow explanation linking randomized groups to the efficacy population. The original statistical analysis plan, interim analysis methods, and any adjustment for baseline values or other covariates are not reported in the registry record. These omissions limit assessment of whether the posted summaries capture the full planned analysis.

14. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gastroenteritis (4.8%), localised infection (4.8%), pneumonia (4.8%), rib fracture (4.8%), drug abuse (4.8%).

The registry reports serious adverse event figures as participants at risk and participants affected. In the high-dose group, 43 were at risk and 4 were affected. In the low-dose Engensis-and-placebo group, 39 were at risk and 3 were affected. In the placebo group, 21 were at risk and 3 were affected. Deaths are reported as 0 in each group. These figures are descriptive; they do not establish that an event was caused by an intervention.

The listed serious-event terms include Gastroenteritis, Localised infection, Pneumonia, Rib fracture, and Drug abuse, each reported at 4.8%, and Omental infarction, reported at 2.6%. The registry does not map these terms to a particular treatment group in the posted term list, so group-specific attribution should not be inferred. It also does not give enough detail in this record to assess event timing, duration, relatedness, or differences in follow-up exposure.

Other adverse event figures are also listed: 33 affected in the high-dose group, 22 in the low-dose Engensis-and-placebo group, and 13 in the placebo group, with the corresponding at-risk counts stated above. These are counts, not comparative risk estimates. No additional rates or group comparisons are calculated.

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

The posted results describe changes in average pain scores among the specified efficacy population and provide unadjusted recalculated comparisons. They show negative mean changes in all three groups. The comparison estimates are positive relative to the low-dose Engensis-and-placebo reference, with intervals that include zero. The data therefore leave uncertainty about the direction and size of the between-group differences under these simple calculations.

These results do not, by themselves, establish whether Engensis is effective or ineffective. They are not a medical recommendation, and group averages do not describe every participant's experience. A change within a group cannot establish that the assigned intervention caused the change. Comparisons between randomized groups can be informative, but their interpretation depends on the analysis population, follow-up, missing-data methods, and statistical plan. Several of those details are not reported in the registry record.

The posted comparisons use the low-dose Engensis-and-placebo arm as the reference for both contrasts, rather than reporting a direct contrast of each active dose with saline placebo. This makes the comparison structure less straightforward than the study's placebo-controlled title suggests. The endpoint timing is also inconsistent: the title, timeframe, and description refer to different or conflicting follow-up points. These limitations affect the specific question that can be answered from the posted data.

The outcome is measured on a 0-to-10 pain scale, but the registry does not report a threshold for a clinically important change. Statistical differences, even if established by a fuller analysis, would not by themselves determine clinical importance. The posted estimates should be understood as summaries with uncertainty, not as definitive evidence about individual benefit, harm, or the best treatment choice.

16. Why This Trial Matters Statistically

This trial illustrates why the comparison being estimated matters as much as the outcome itself. The study is described as placebo-controlled, but the posted recalculated comparisons use the low-dose Engensis-and-placebo arm as the reference for both comparisons. A reader seeking a direct active-treatment-versus-saline estimate should not interpret these contrasts as though that were what they represent.

It also highlights the difference between a within-group change and a between-group comparison. All three group means are negative, but that alone cannot distinguish changes associated with treatment assignment from changes that may occur for other reasons. Between-group estimates are more relevant to comparative questions, yet the reported intervals are broad enough to include zero and the calculations are unadjusted.

The registry's endpoint timing inconsistency is important for reproducibility. A change measured at the 6-month follow-up is not necessarily the same estimand as a change associated with the 9 Month visit. Statistical summaries need a clearly specified measurement period to support consistent interpretation across analyses.

Finally, the efficacy population excludes people without the specified Day 180 assessment and those with protocol violations or major deviations. Without participant-flow details or missing-data analyses, it is difficult to assess how this selection affects the results. These are general concerns in clinical-trial interpretation, made concrete by the limited information in this record. The posted results are useful as a description of the recorded estimates, while leaving important design and analysis questions unresolved.

17. 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 has several trial-specific limitations for interpreting the posted outcome. First, the primary endpoint timing is inconsistent: its title says change through the 6-month follow-up, its timeframe refers to the seven days before the 9 Month visit, and its description refers to the 6 month follow-up. The record does not clarify which measurement period the reported results represent.

Second, the posted comparison calculations use the low-dose Engensis-and-placebo group as the reference for both contrasts. They do not provide a direct high-dose-versus-placebo contrast or a direct low-dose-versus-placebo contrast in the posted comparison summaries. The study's placebo-controlled framing therefore does not by itself identify the contrast represented by each estimate.

Third, the outcome population is restricted to subjects who received the correct dose at both dosing days, had a Day 180 assessment, and had no protocol violations or major deviations. Participant flow from enrollment to these arm-level endpoint summaries, reasons for exclusions, and missing-data methods are not reported in the registry record. This limits evaluation of selection and attrition.

The original sample-size justification, statistical analysis plan, adjusted analyses, multiplicity procedures, interim analyses, and sensitivity analyses are not reported. The registry also does not specify the confidence level for the recalculated intervals. These omissions mean the summary-statistic recalculations should not be mistaken for the trial's complete planned analysis. Safety-term listings are not linked to treatment groups in the term list, and event timing or relatedness is not posted in the record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Efficacy Study for the Treatment of Painful Diabetic Neuropathy — NCT01475786.
• Registry record last updated 2025-10-06; status last verified 2025-08.
• Results first posted 2023-07-03.
• 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.

21. Record Summary

The registry describes NCT01475786 as a completed, randomized, double-blind, placebo-controlled Phase II study of Engensis (VM202) for painful diabetic peripheral neuropathy. Enrollment is listed as 104. The interventions were low-dose Engensis at 16 mg, high-dose Engensis at 32 mg, and normal-saline placebo. The primary outcome was change in average 24-hour pain score, measured using a daily numerical rating scale.

Posted group means are negative in all three arms. Recalculated unadjusted comparisons use the low-dose Engensis-and-placebo arm as the reference, and both reported intervals include zero. The record defines a selected efficacy population but does not report the full analysis plan, missing-data methods, or multiplicity handling. It also gives conflicting descriptions of the endpoint follow-up timing. Serious adverse event counts and deaths are listed by group, but the serious-event term list is not assigned to particular groups.