D-PLEX 310: Safety and Efficacy of D-PLEX in the Prevention of Post Abdominal Surgery Incisional Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for D-PLEX 310: Safety and Efficacy of D-PLEX in the Prevention of Post Abdominal Surgery Incisional Infection (NCT03633123), a randomized phase 2 study. The primary outcome is The Combined Infection and Mortality Rate Within 30 Days Post Index Surgery.

2. Clinical Question

The primary outcome combines two different events: a surgical-site infection (SSI) and death from any cause. An event was counted when either occurred within the stated 30-day period. SSI was determined by a blinded, independent adjudication committee, according to the registry description. The composite therefore addresses whether participants experienced at least one of the specified outcomes, rather than measuring infection alone.

The trial record describes planned abdominal, including colon, surgery and random allocation to the two treatment groups. It identifies the study as phase II and the condition context as abdominal surgery, colon surgery, and postoperative infection. The record does not report further detail about eligibility criteria, such as the complete inclusion and exclusion rules. It also does not report the rationale for combining infection and mortality in one primary outcome or how the study handled a participant who experienced both. The principal comparison is the posted event count in each group and the associated effect estimate, with uncertainty considered alongside the observed difference.

3. Trial Design

NCT03633123 is recorded as a completed, phase II, randomized, parallel-group study sponsored by PolyPid Ltd. The registry gives an enrollment of 202 and describes two arms: D-PLEX plus SoC and SoC alone. The posted primary-outcome denominators are 101 and 100, respectively. The record lists allocation as randomized and masking as double; however, the official title calls the study single blind. That difference in masking descriptions is present in the registry record and is not resolved there.

The planned population consisted of people undergoing abdominal, specifically colon, surgery who met the entry criteria. In the D-PLEX group, D-PLEX was added to SoC. The SoC arm received prophylactic treatment before the operation, described as a first- or second-generation cephalosporin plus metronidazole, consistent with Israeli Ministry of Health and international guidelines. After surgery, participants were to have five additional follow-up visits, with at least half described as aligned with routine surgical follow-up. Visits included patient-safety and wound assessments.

The registry records the study start as 2018-10-04, primary completion as 2019-09-06, and status as completed. The primary population is identified as ITT. The record does not report the details of the randomization procedure, allocation concealment, the exact masking roles, or whether any participants discontinued or were excluded from particular analyses. Nor does it report the original protocol’s statistical analysis plan or the study’s own assumptions for its planned sample size. These omissions limit assessment of how the trial was planned and conducted beyond the information recorded in the registry.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to Treat (ITT) population.

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: One subject was excluded from the ITT population (SoC arm) as was not undergo abdominal surgery and had no abdominal incision to evaluate.

6. Primary Endpoint

The registry lists the primary outcome as The Combined Infection and Mortality Rate Within 30 Days Post Index Surgery, measured over 30 days post surgery.

The primary endpoint is the combined infection and mortality rate within 30 days after index surgery. It is expressed as the number of participants with either an SSI event or death from any cause during that period. The registry states that SSI events were determined by a blinded, independent adjudication committee. The analysis population is the ITT population.

A composite endpoint can capture more than one clinically relevant type of event in a single comparison. It can also make the result harder to interpret: infection and death differ in nature, and a group-level composite does not by itself reveal which component accounts for the pattern. The infection count and mortality count should therefore be considered separately where the registry posts them, as well as in relation to the combined primary outcome. The record does not report a component-specific analysis of the primary endpoint or how participants with both events were counted.

The primary result is a comparison of event counts between randomized groups. The risk difference expresses the absolute contrast between their event proportions; a negative value in the direction used for this comparison indicates a lower observed proportion in the D-PLEX plus SoC group. The estimate should be read together with its interval, which conveys uncertainty, and the sponsor’s reported analysis. The endpoint describes what was recorded during the specified follow-up window. It does not establish the effect on outcomes beyond that period, nor does the composite alone identify the contribution of each component.

7. Results Posted in the Registry

• D-PLEX + SoC: 9.9% (10/101) versus 24.0% (24/100) on control; risk difference -14.1 percentage points (95% CI -24.3 to -3.9), risk ratio 0.41 (0.21–0.82); unadjusted two-proportion z-test p = 0.008.

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.

Average ASEPSIS Assessment Score (for Parameters Additional Treatment, Serous Discharge, Erythema, Purulent Exudate, Separation of Deep Tissue, Isolation of Bacteria, Stay Duration as Inpatient) During 30 Days Post-surgery.

• 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:
  • D-PLEX + SoC: mean 0.77 versus 1.37 on control; difference -0.60 (95% CI -1.73 to 0.53), standardized effect d = -0.15; z-test p = 0.298.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between D-PLEX + SoC and the control. The interval gives the range of effects that remain compatible with the data.

Mortality Rate Within 30 Days Post Abdominal Surgery

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • D-PLEX + SoC: 0.0% (0/101) versus 3.0% (3/100) on control; risk difference -3.0 percentage points (95% CI -6.3 to 0.3); unadjusted two-proportion z-test p = 0.079.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between D-PLEX + SoC and the control. The interval gives the range of effects that remain compatible with the data.

The two posted secondary outcomes add context to the primary composite but do not simply replicate it. One concerns average ASEPSIS assessment scores over the 30 days after surgery, while the other reports mortality over the same stated period. The endpoints use different measurement scales and address different aspects of postoperative outcome, so they should not be combined informally or treated as interchangeable checks on the primary result.

The pattern across the secondary outcomes is not uniformly conclusive: the recalculated score comparison has an interval that includes zero, as does the mortality comparison. The mortality counts also appear in the serious-adverse-event information, but those listings do not have matching numbers of deaths. The record does not explain the difference in definitions, analysis population, or time window between those entries. That ambiguity limits how confidently the safety listing can be used to interpret the secondary mortality endpoint.

Secondary results can help describe the broader outcome profile and may generate questions for further study. They carry less weight as confirmatory evidence when no adjustment or prespecified testing hierarchy is reported. Testing multiple outcomes can increase the chance of apparently noteworthy results arising through chance alone. The registry reports 14 outcome measures but posts results for two secondary outcomes; it does not report the full multiplicity plan or how unposted measures were handled. Accordingly, secondary findings should be viewed as supportive or exploratory rather than as independent confirmation of the primary comparison.

The secondary endpoints do not overturn the primary result, nor do they establish that its effect extends to every postoperative outcome. The composite, score, and mortality comparisons answer separate questions. Their interpretation depends on endpoint definitions, completeness of follow-up, and the analysis methods, some of which are not reported in the registry record.

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

• Average ASEPSIS Assessment Score (for Parameters Additional Treatment, Serous Discharge, Erythema, Purulent Exudate, Separation of Deep Tissue, Isolation of Bacteria, Stay Duration as Inpatient) During 30 Days Post-surgery.
• Mortality Rate Within 30 Days Post Abdominal Surgery

9. Statistical Interpretation

10. Statistical Methods Explained

The primary and mortality outcomes are binary: each participant either met the outcome definition within the stated follow-up period or did not. The record posts counts and denominators by group. The recalculated comparisons use those posted summaries and are unadjusted. That means the estimates describe the direct group contrast without adjustment for other participant characteristics. The registry does not report whether the sponsor’s analysis used additional adjustment.

What does a risk difference express?

A risk difference is the event proportion in one group minus the event proportion in the comparison group, with the direction determined by the comparison as defined. It gives an absolute contrast on the proportion scale. For the primary outcome, the recalculated estimate is -0.141. Its negative sign indicates a lower observed event proportion in the D-PLEX plus SoC group relative to SoC in this calculation. A risk difference is distinct from a risk ratio: the difference describes an absolute gap, while the ratio compares the proportions relative to one another. The sponsor reported a risk ratio of 0.41 rather than a risk difference.

What does a confidence interval convey?

A confidence interval expresses uncertainty around an estimate using a method with specified statistical properties. A narrower interval indicates greater precision under that method; a wider interval indicates less precision. For a risk difference, zero represents no difference between the group proportions. The recalculated primary interval runs from -0.243 to -0.039 and does not include zero. By contrast, the intervals for the recalculated mortality and mean-score comparisons include their respective null values. An interval is not a guarantee that the true effect lies within its limits, and it does not replace consideration of design, measurement, or analysis limitations.

Why is Fisher’s exact test reported?

The sponsor reports a Fisher Exact analysis for the risk ratio, with p = 0.009. Fisher’s exact test is a method for assessing evidence against a null association in a two-group comparison of categorical outcomes. It calculates a tail probability under the null model and the test’s assumptions. A p-value is not the probability that the null hypothesis is true, nor is it a measure of the size or importance of an effect. The registry does not provide the sponsor’s confidence-interval limits for the risk ratio. Its reported result should therefore be read with the displayed risk-ratio estimate and the separate recalculated risk-difference interval, recognizing that they are different measures.

How should the continuous outcome be read?

The ASEPSIS assessment is reported as a mean and standard deviation in each group. The recalculated mean difference is -0.6, based on the group means of 1.37 and 0.77, and its interval includes zero. A mean difference describes the contrast in average scores. The standard deviation describes variation among scores within a group; it is not the uncertainty interval for the group mean or the estimated difference. The reported standard deviations, 4.72 and 3.32, are large relative to the means. In general, substantial variation can make a mean difference harder to estimate precisely, especially when the sample is limited. The registry does not report the score distribution, score range, or whether any transformation or alternative analysis was considered.

The recalculated mean comparison is based on an unadjusted method using posted summary statistics. The record gives a pooled standard deviation of 4.077 for the planning calculations and indicates that the standard deviation was not approximated. These details describe the calculation used for planning illustrations; they do not establish the original trial’s analysis plan. The reported comparison has an unadjusted p-value of 0.298. It should not be interpreted as proof that the groups are identical: the estimate has uncertainty, and a failure to distinguish a difference from zero is not evidence that every possible difference has been excluded.

Why can over-dispersion matter?

Over-dispersion is a general concern when variability in data is greater than a statistical model assumes. If a model understates variability, standard errors can be too small and intervals too narrow, making results appear more precise than they are. The posted ASEPSIS standard deviations describe variation, but the registry does not report a formal assessment of over-dispersion, the score distribution, or a model-based analysis. It would therefore be inappropriate to claim that over-dispersion was present or that a particular correction was needed. The general point is that the analysis method should reflect the data’s variability and scale.

All recalculated p-values and intervals are unadjusted. The registry lists one reported primary analysis and two posted secondary endpoints, but it does not report how multiplicity was addressed or whether a prespecified hierarchy governed interpretation. If many outcomes are tested, the chance of at least one apparently unusual result can increase. General methods to address this include prespecified outcome hierarchies or multiplicity adjustments, but the record does not say that any such method was used. The posted p-values should consequently be interpreted as outcome-specific rather than as evidence that a family of results has been controlled for multiple testing.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.141, with an interval from -0.243 to -0.039. The estimate is directionally in favor of a lower observed event proportion in the D-PLEX plus SoC group, and the interval does not include zero. Its limits nevertheless allow a range of effect sizes; the point estimate is not a precise prediction of what would occur in another study or population. The interval’s interpretation depends on the statistical method and assumptions used in the recalculation.

The sponsor reports a risk ratio of 0.41 and identifies a 95% confidence level for its analysis, but the record does not give the interval limits. The sponsor’s p-value is 0.009. The risk ratio is a relative measure, whereas the recalculated risk difference is an absolute measure; they answer related but distinct questions. The registry does not flag a discrepancy between the sponsor’s analysis and the recalculation.

For mortality, the recalculated risk-difference interval includes zero, and the unadjusted p-value is 0.079. For the mean ASEPSIS score, the interval also includes zero, with an unadjusted p-value of 0.298. In general, an interval that includes a null value indicates that the data and method do not rule out that value at the interval’s level. It does not prove the null value is correct, and it may still be compatible with effects in more than one direction.

Precision is affected by the number of observations, the frequency of events, and variability in measurements. The posted denominators are 100 and 101 for the primary outcome, while the mortality and continuous outcomes have their own reported denominators and outcome characteristics. Rare events can yield especially uncertain estimates, even when the counts differ between groups. The record does not report the confidence level for the recalculated intervals or the method used to construct them. The intervals are therefore best read as uncertainty summaries accompanying the posted recalculations, not as complete descriptions of all sources of uncertainty.

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 illustrations based on the observed effect, not the trial’s original design assumptions. For these outcomes, the figures are participants per arm; the record specifies total events only for time-to-event calculations, and these analyses are not time-to-event outcomes. The 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 the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were present. The 90% power column describes the corresponding planning target for a 90% chance. These are design targets, not guarantees that a study will detect an effect. They also do not describe the chance that the observed trial result is true.

For the primary outcome, the planning illustration gives 110 participants per arm for 80% power and 147 for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the figures are 213 and 284; for 50% of the observed effect, they are 514 and 687. The ASEPSIS-score illustrations are larger: for 100% of the observed effect, they give 725 and 971 participants per arm; for 75%, 1,289 and 1,725; and for 50%, 2,900 and 3,882.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of an observed effect requires more participants under the stated assumptions. These figures are not observed power. They are illustrative future-planning calculations based on effects observed in this trial, which are themselves uncertain; they should not be read as evidence that the completed trial had a particular probability of success.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.240; treatment proportion p₁ = 0.099; average p̄ = 0.170.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5306 = 1.0400.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5212 = 0.4386.
4. n = (1.0400 + 0.4386)² / (-0.1410)² = 110.0, rounded up to 110 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.24                          # control proportion
p1 <- 0.099009900990099                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3633123)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 110 (80% power), 147 (90% power)
 75% of observed effect: n per arm = 213 (80% power), 284 (90% power)
 50% of observed effect: n per arm = 514 (80% power), 687 (90% power)
power.prop.test: 110 
Simulated power at n = 110 per arm: 0.814 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s own reported primary analysis uses Fisher’s exact test and reports a risk ratio of 0.41 with p = 0.009. The registry does not give confidence-interval limits for that risk ratio. Separately, the unadjusted recalculation from the posted counts gives a risk difference of -0.141, an interval from -0.243 to -0.039, and p = 0.008. These are different effect measures, so the numerical estimates should not be compared as if they were on the same scale.

The sponsor’s result and the recalculation both indicate a lower observed event proportion in the D-PLEX plus SoC group for the primary outcome, but the sponsor’s analysis remains the trial’s own reported analysis. The registry’s discrepancy flag is false, so no disagreement is flagged between the sponsor analysis and the recalculation. This does not make the unadjusted recalculation a replacement for the trial analysis; it is a separate calculation from the posted summary counts.

The record does not provide details of the sponsor’s full statistical analysis plan, adjustments, or the basis for selecting Fisher’s exact test. It also does not provide a reported confidence interval for the sponsor’s risk ratio. Readers should therefore distinguish the sponsor’s inferential analysis from the simpler recalculation and consider both alongside the endpoint definition, population, and limits of the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and posts two secondary outcomes. It also states that 14 outcome measures were included, while only two secondary outcomes appear in the posted outcome results. The record does not report a multiplicity adjustment, a testing hierarchy, or a rule specifying how secondary analyses were to be interpreted. It is therefore unclear whether the reported p-values were intended as confirmatory tests within a controlled family of hypotheses or as separate exploratory comparisons.

Multiplicity matters because testing multiple outcomes can increase the chance of at least one small p-value even when no corresponding effect exists. In general, a prespecified hierarchy or statistical adjustment can address this issue, but the registry does not report whether either was used. The posted unadjusted secondary p-values should not be treated as if they automatically account for the number of outcomes examined.

The primary analysis population is identified as ITT. The registry does not report how missing outcome data were handled, whether participants were lost to follow-up, whether any participants were excluded from particular analyses, or whether sensitivity analyses assessed alternative assumptions about missingness. It also does not report the amount or pattern of missing data. These details matter because outcome availability can affect both the group denominators and the conclusions, especially if missingness differs between groups or is related to outcome status.

The record does not report interim analyses, stopping rules, or the original statistical analysis plan. It also does not report a specific sample-size justification for the trial; the planning calculations associated with the posted results are illustrations based on observed effects, not the original design. These are gaps in the available registry information, not evidence that a particular procedure was or was not used. The primary result can be described from the posted data, but a fuller assessment of prespecification, multiplicity control, and missing-data robustness is not possible from this record alone.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anastomotic leak (3.0%), ileus (2.0%), small intestinal obstruction (2.0%), postoperative wound infection (2.0%), internal hernia (1.0%).

The serious adverse event information lists 20 affected participants among 100 at risk in the SoC group and 16 among 99 at risk in the D-PLEX plus SoC group. Other adverse events are listed for 52 participants among 100 at risk in the SoC group and 50 among 99 at risk in the D-PLEX plus SoC group. These are descriptive registry counts; they do not by themselves show that an event was caused by a study treatment.

The listed serious terms include anastomotic leak at 3.0%, ileus at 2.0%, small intestinal obstruction at 2.0%, postoperative wound infection at 2.0%, internal hernia at 1.0%, and intestinal obstruction at 1.0%. The record does not provide enough detail to determine the event-level coding, overlap among terms, or the denominator used for each listed percentage. The terms should be read as the registry’s reported safety categories, not as mutually exclusive counts.

The adverse-event listing reports deaths of 5 in the SoC group and 0 in the D-PLEX plus SoC group, while the secondary mortality endpoint reports 3 and 0. The registry does not explain this difference or report whether the entries use different populations, definitions, or time periods. The two death counts should not be treated as interchangeable. Safety counts are descriptive and do not establish comparative causation or a complete safety profile.

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

The posted primary result shows fewer recorded participants with the combined infection-or-death outcome in the D-PLEX plus SoC group than in the SoC group. The recalculated risk difference is -0.141, and its interval does not include zero. The sponsor’s reported risk ratio is 0.41 with p = 0.009. These results describe this randomized comparison and the defined 30-day endpoint; they do not establish what would happen in every setting or population.

The primary endpoint combines SSI and death from any cause. Its result does not reveal, on its own, how much each component contributed. The separately posted mortality outcome has few events and an interval that includes zero. The record does not report a component-specific analysis of the primary composite, so the combined finding should not be interpreted as a separate estimate of infection alone.

Statistical evidence and practical importance are different questions. An effect estimate describes the size and direction of a comparison, while its interval describes uncertainty under the analysis method. A p-value addresses compatibility with a null model, not the probability that a treatment works or the size of a benefit. The registry does not report a threshold for clinical importance, nor does it provide enough information to assess all possible sources of bias, missing data, or outcome-measurement limitations.

The completed phase II trial contributes a randomized comparison in the stated surgical setting. The posted outcomes do not establish longer-term effects because the primary window is 30 days after surgery, and the record does not report longer-term results. The findings also do not replace evaluation of the adverse-event record or of the limitations in the registry information. They describe observed outcomes and statistical uncertainty; they are not medical advice or a recommendation about treatment.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares an adjunctive intervention with standard care using randomized allocation and a clearly stated primary time window. Randomization is intended, in general, to make treatment groups comparable on average, reducing the risk that measured or unmeasured baseline factors systematically determine group assignment. The registry identifies the study as randomized, but it does not report the randomization sequence or allocation-concealment details needed to assess those procedures fully.

The primary outcome illustrates why effect measures and uncertainty need to be read together. The risk difference gives an absolute comparison, while the sponsor’s risk ratio gives a relative comparison. Both concern the same combined outcome, but they communicate different aspects of the contrast. The primary recalculated interval excludes zero, whereas the secondary intervals include their null values. This contrast demonstrates why conclusions should be specific to the endpoint and analysis rather than generalized across all outcomes.

The composite endpoint also raises a general interpretive issue: a single summary can combine events with different meanings. The infection and mortality components are both relevant to the stated question, but a combined estimate cannot show which component drives the result. The separately reported mortality outcome helps add context, while the inconsistent death counts in the safety and secondary listings make the registry’s definitions and analysis populations important to clarify.

Finally, the planning illustrations show how sample-size requirements depend on the effect targeted and the outcome’s variability. They are based on observed effects and are not the study’s original design justification. This distinction matters when interpreting a completed trial: an observed estimate can be uncertain, and planning calculations derived from it should not be mistaken for evidence about the trial’s original power or success probability.

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.

Several trial-specific limitations follow from the registry information. The official title describes the study as single blind, whereas the masking field lists double masking. The record does not explain this inconsistency or identify which participants, investigators, or assessors were masked. Although the primary SSI outcome is described as determined by a blinded and independent adjudication committee, the broader masking arrangements remain unclear.

The primary outcome is a composite of SSI and death from any cause, but the record does not post a component-specific breakdown for the primary analysis or explain how participants with both events were counted. The separate mortality endpoint and the adverse-event death listing contain different SoC counts, 3 and 5, respectively. The registry does not explain whether that difference reflects outcome definitions, populations, or time windows. These details should be clarified before treating the listings as consistent accounts of mortality.

The record does not report the original sample-size justification, the statistical analysis plan, multiplicity procedures, interim analyses, missing-data handling, or sensitivity analyses. It also does not report complete eligibility criteria, baseline characteristics, or detailed follow-up completion. The available endpoint summaries therefore cannot establish how robust the estimates are to missing outcomes or analytic choices.

Generalizability is also bounded by the registered setting: planned abdominal, specifically colon, surgery, with SoC described according to Israeli Ministry of Health and international guidance. The record does not provide enough detail to characterize the full range of patients or clinical settings represented. These limitations do not negate the posted comparison, but they constrain how broadly it can be interpreted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: D-PLEX 310: Safety and Efficacy of D-PLEX in the Prevention of Post Abdominal Surgery Incisional Infection — NCT03633123.
• Registry record last updated 2026-03-24; status last verified 2026-03.
• Results first posted 2026-03-24.
• 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

NCT03633123 is a completed phase II randomized, parallel-group study sponsored by PolyPid Ltd. It compares D-PLEX added to SoC with SoC alone in people planned for abdominal, specifically colon, surgery. The registry records an enrollment of 202, a start date of 2018-10-04, and primary completion on 2019-09-06.

The primary outcome is the combined rate of SSI or death from any cause within 30 days after surgery, analysed in the ITT population. The registry reports 24 primary events in the SoC group and 10 in the D-PLEX plus SoC group. The sponsor reports a risk ratio of 0.41 and p = 0.009; the unadjusted recalculation gives a risk difference of -0.141 with an interval from -0.243 to -0.039 and p = 0.008.

Two secondary outcomes are posted: average ASEPSIS score and mortality. The registry does not report the original sample-size rationale, missing-data methods, multiplicity plan, or full statistical analysis plan. It also contains differing masking descriptions and differing death counts across the secondary and safety listings, which are not explained in the record.