A Study to Evaluate Two Different Surgical Methods for Treatment for Abdominal Wall Diastasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate Two Different Surgical Methods for Treatment for Abdominal Wall Diastasis (NCT01586741), a randomized na study. The primary outcome is Recurrence of Diastasis One Year Post-operatively That Indicated by CT Scan or Clinical Investigation..

2. Clinical Question

3. Trial Design

NCT01586741 is recorded as a prospective randomized study with a parallel-group model and single masking. The study title identifies a comparison of two surgical methods for abdominal wall diastasis, and the registry describes three arms: polypropylene mesh, Quill suture, and conservative treatment. The record lists the phase as not applicable. Karolinska Institutet is named as the sponsor.

The registry gives enrollment as 96 and status as completed. The recorded study start was 2009-12 and primary completion was 2011-11. Arm descriptions state that 30 patients were intended for each treatment. For the posted primary outcome, the reported denominators are 29.0 for polypropylene mesh, 27.0 for Quill suture, and 30.0 for conservative treatment. The registry does not explain why these outcome denominators differ from the arm descriptions, or whether any participants were excluded from the primary outcome analysis.

The surgical arms differed by the material and technique used for reconstruction: polypropylene mesh or double-row absorbable Quill suture. Conservative treatment consisted of regular abdominal exercise for three months. The primary outcome was assessed at follow-up one year after surgery using CT scan or clinical investigation. The record also lists postoperative pain measured by VHPQ questionnaires and adverse events indicated in the case report form during the first 12 months as secondary outcomes. Results for those secondary outcomes are not reported in the registry record.

Further details about the randomization procedure, masking procedures, recruitment setting, and participant characteristics are not reported in the registry record. The record also does not describe the protocol’s planned statistical methods or its original assumptions for choosing the study size.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Recurrence of Diastasis One Year Post-operatively That Indicated by CT Scan or Clinical Investigation., measured over follow-up 1 year after surgery.

The primary endpoint was recurrence of diastasis one year after surgery, assessed by CT scan or clinical investigation. The registry reports this outcome as a count of participants with recurrence, rather than as a continuous measurement such as a change in abdominal separation. In the posted results, the polypropylene mesh arm had 2.0 participants with the event among 29.0, the Quill suture arm had 3.0 among 27.0, and the conservative treatment arm had 26.0 among 30.0.

Recurrence is a clinically interpretable outcome for a study comparing methods intended to address abdominal wall diastasis: it records whether the condition was identified again at follow-up. Using both CT scanning and clinical investigation offers two stated ways of assessing the outcome. The registry does not give further detail about how the two assessment methods were combined, how recurrence was defined on imaging or examination, or how disagreements were handled. Those measurement details are not reported in the registry record.

As a general statistical point, a binary endpoint reduces each participant’s outcome to whether the event was recorded or not. This supports direct comparison of event frequencies between groups, but it does not describe the severity of recurrence, the timing of an event within follow-up, or changes in symptoms. The primary endpoint should therefore be interpreted as recurrence status at the specified follow-up, not as a complete account of all aspects of recovery or treatment experience.

7. Results Posted in the Registry

• Quill Suture: 11.1% (3/27) versus 6.9% (2/29) on control; risk difference 4.2 percentage points (95% CI -10.8 to 19.2), risk ratio 1.61 (0.29–8.91); unadjusted two-proportion z-test p = 0.580.
• Conservative Treatment: 86.7% (26/30) versus 6.9% (2/29) on control; risk difference 79.8 percentage points (95% CI 64.5 to 95.0), risk ratio 12.57 (3.28–48.21); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant is classified according to whether recurrence was recorded. For this type of endpoint, a group’s event count is interpreted relative to its reported outcome denominator. The count alone does not say how frequent the event was without the denominator; conversely, a percentage alone would conceal how many participants contributed to it. The registry reports counts and denominators for each arm, allowing the primary outcome to be read as participant events rather than as a continuous score.

The main absolute comparison is the risk difference. In plain terms, it is the event risk in one arm minus the event risk in the reference arm. The sign indicates the direction of the contrast under that ordering: positive estimates mean a higher estimated recurrence risk in the named comparison arm than in mesh. A risk difference of zero represents no estimated absolute difference. This measure is often useful for clinical interpretation because it expresses the contrast on the event-risk scale. The registry lists polypropylene mesh as the control arm for both comparisons.

A confidence interval around a risk difference describes a range of values compatible with the data under the method used to construct the interval. It conveys uncertainty in the estimated contrast, not a range containing a guaranteed proportion of future results and not the probability that a treatment effect is within the interval. If an interval spans zero, the data are compatible with no difference as well as with effects in either direction at the interval’s stated level. If the interval lies entirely on one side of zero, it indicates that the estimates covered by that interval have the same direction. Interval width also matters: wider intervals indicate less precision. The registry does not report which specific interval construction method was used.

The risk ratio and odds ratio are relative measures, also reported for the two comparisons. A risk ratio compares the event risks directly; a value of one corresponds to equal risks. An odds ratio compares event odds rather than risks, and a value of one corresponds to equal odds. These measures can be useful complements to a risk difference, but they answer questions on different scales and are not interchangeable. When outcomes are common, an odds ratio can appear more extreme than a risk ratio. The registry’s conservative-treatment event count is large relative to its denominator, so the odds ratio should not be read as if it were a risk ratio.

The p-values in the record are unadjusted. A p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, nor is it a measure of effect size. The registry does not identify the test or model used to produce the p-values, or state the assumptions used for those tests. Consequently, the p-values should be read as posted, without attributing a particular statistical procedure to the analysis.

The study is described as randomized, which is relevant because random allocation is intended to make comparison groups similar on average before treatment. However, the registry does not report the allocation sequence method, concealment method, or detailed masking procedures. The record identifies single masking but does not specify who was masked. Randomization alone does not resolve questions about missing outcome data, departures from assigned treatment, outcome assessment, or analysis population; those details are not reported in the registry record.

There are two posted primary comparisons against the mesh reference. Conducting multiple comparisons can increase the chance that at least one result appears statistically unusual by chance. A prespecified multiplicity strategy may address that issue, but such a strategy is not reported in the registry record. The displayed p-values are explicitly unadjusted, so they should not be interpreted as multiplicity-adjusted evidence. The record does not report whether the primary comparisons were specified in advance or whether any other analyses were planned.

As a general statistical consideration, binary outcomes can be analyzed with different methods, and the method can matter when group counts are limited or event frequencies are very different. The registry does not say whether an exact test, a large-sample test, a regression model, or another approach was used. It also does not report adjusted estimates, covariates, a formal analysis plan, or the handling of missing outcomes. The posted estimates therefore support descriptive interpretation of the recorded comparisons, while the exact inferential method and analysis details remain unclear.

Over-dispersion is a concern mainly for count models in which observed variation exceeds the variation assumed by a simple model; accounting for it can avoid overly narrow uncertainty estimates. This endpoint is posted as participant event counts, not as a repeated count outcome, and the registry does not report a count-model analysis. There is therefore no basis in the record to say that an over-dispersion adjustment was used or needed for the posted primary comparison. More generally, the suitability of any model depends on the data structure and prespecified analysis, neither of which is described in detail.

All numerical comparisons should be separated from questions of clinical importance. Statistical evidence about a difference does not establish that the difference is large enough to matter to patients, and a non-significant result does not demonstrate equivalence. Equivalence or non-inferiority requires a design and margins specified for that purpose; such margins are not reported in the registry record. The record’s stated primary question and posted risk differences do not establish that such an analysis was planned.

10. Confidence Intervals and Precision

The Quill suture versus mesh risk difference is 0.042, with a 95% confidence interval from -0.108 to 0.192. This interval crosses zero, so it is compatible with no absolute difference as well as with differences in either direction. Its width indicates substantial uncertainty about the size and direction of the contrast. The relatively close event counts do not make the estimated comparison precise, because the outcome denominators are limited and the confidence interval remains broad.

For conservative treatment versus mesh, the risk difference is 0.798, with a 95% confidence interval from 0.645 to 0.950. This interval lies entirely above zero, so the posted estimate is consistent with a higher recurrence risk in the conservative arm. Its lower and upper limits still span a range of possible magnitudes, which means the precise size of the difference is uncertain even though the interval does not cross zero.

The relative-measure intervals reinforce the need to consider uncertainty alongside point estimates. For Quill suture versus mesh, the risk-ratio interval ranges from 0.291 to 8.914, and the odds-ratio interval ranges from 0.260 to 10.97. Both cover the null value of one and allow for substantial variation in the relative contrast. For conservative treatment versus mesh, the risk-ratio interval ranges from 3.275 to 48.21, while the odds-ratio interval ranges from 14.79 to 520.7. These intervals are wide, so the relative magnitude is imprecisely estimated.

A confidence interval is not a guarantee about the true value, and its interpretation depends on the method and assumptions used to calculate it. The registry does not report the interval method. Precision is also distinct from clinical importance: an estimate can be precise but clinically small, or large but uncertain. The posted primary results give clearer directional evidence for the conservative-treatment comparison than for the Quill comparison, while uncertainty remains about the exact effect size, especially on relative scales.

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 based on the observed effect, rather than the study’s original design calculation. The stated 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 to the stated fraction of the observed effect. The registry record does not report the original protocol’s sample-size assumptions or justification.

For each displayed effect size, the 80% power column gives the planned participants per arm under those assumptions to have an 80% chance of detecting an effect of that size, if the assumed effect and statistical model apply. The 90% power column gives the corresponding participants per arm for a higher target chance of detection. These are prospective planning quantities, not properties of the observed analysis. This is not observed power.

The planning values vary greatly by comparison. For the Quill-versus-mesh observed effect, the figures are 723 participants per arm for 80% power and 968 for 90% power when planning for 100% of the observed effect. Planning for 75% gives 1,218 and 1,630, while planning for 50% gives 2,586 and 3,462. For conservative treatment versus mesh, the corresponding figures are 5 and 6 for 100%, 9 and 12 for 75%, and 19 and 24 for 50%.

These are illustrations tied to the observed effects in this study. A smaller effect is harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm under the stated assumptions. The unusually large contrast in the conservative-treatment comparison yields much smaller illustrative sample sizes than the smaller Quill comparison; that contrast should not be mistaken for a general expectation in a future study.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.069; treatment proportion p₁ = 0.111; average p̄ = 0.090.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4048 = 0.7934.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4037 = 0.3398.
4. n = (0.7934 + 0.3398)² / (0.0421)² = 722.9, rounded up to 723 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 <- 0.0689655172413793                          # control proportion
p1 <- 0.111111111111111                          # 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(1586741)
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 = 723 (80% power), 968 (90% power)
 75% of observed effect: n per arm = 1,218 (80% power), 1,630 (90% power)
 50% of observed effect: n per arm = 2,586 (80% power), 3,462 (90% power)
power.prop.test: 722.9 
Simulated power at n = 723 per arm: 0.797 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry reports two primary comparisons against polypropylene mesh: Quill suture versus mesh and conservative treatment versus mesh. The p-values are unadjusted. When several comparisons are made, the chance of at least one false-positive finding can be greater than when a single comparison is made. Statistical plans can address multiple comparisons through prespecified procedures, but the registry record does not report whether an adjustment was planned or used. The posted p-values should therefore be interpreted as unadjusted rather than as evidence corrected for multiplicity.

The record does not report whether the primary endpoint, comparison ordering, or analysis method was prespecified in a protocol or statistical analysis plan. It also does not describe any interim analyses, stopping rules, or subgroup analyses. These details are not reported in the registry record, so no assumptions should be made about their use.

The outcome denominators are 29.0 for mesh, 27.0 for Quill suture, and 30.0 for conservative treatment, while the arm descriptions specify 30 patients for each group. The registry does not explain the difference between those planned arm descriptions and the posted outcome denominators. It does not state whether any outcomes were missing, whether participants were excluded, or how incomplete follow-up was handled. The record also does not identify an intention-to-treat, per-protocol, or other analysis population.

Missing outcome data can affect a comparison if outcome availability is related to treatment or recurrence. The impact depends on why observations are absent and how they are handled; no missing-data method or sensitivity analysis is reported. The record also does not report whether participants received their assigned intervention, crossed between arms, or were analyzed according to assignment. Such information would help readers assess whether the posted comparisons preserve the randomized design.

Secondary outcomes include adverse events during the first 12 months and postoperative pain measured by VHPQ questionnaires. Although the registry lists these outcomes, their results are not reported in the registry record. It is not possible to assess the number of secondary analyses conducted, whether they were adjusted for multiplicity, or how missing secondary outcome information was handled.

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 0% reporting threshold.

The registry reports zero serious adverse events for Quill suture, polypropylene mesh, and conservative treatment. The corresponding serious-adverse-event denominators are 27, 29, and 30 participants at risk. It also reports zero other adverse events in each arm, using the same at-risk denominators. Deaths are reported as zero in all three arms. No serious adverse-event terms are listed.

These figures describe the adverse events entered in the registry for the stated follow-up period; the secondary outcome description refers to events indicated in the case report form during the first 12 months. A zero count means that no events of the specified category were recorded in the posted results. It does not establish that the risk is absent, and it does not rule out events that were not detected, recorded, or included in the registry results.

The denominators are limited, and the record does not provide additional detail about event definitions, severity grading, relatedness assessment, ascertainment procedures, or missing safety data. Zero events in these groups should therefore be read as an observation in this study, not as a conclusive comparison of safety across treatment approaches. The registry does not report detailed safety results beyond these counts.

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

The primary outcome data show a difference in recorded recurrence frequency between the conservative-treatment arm and the mesh arm at one-year follow-up. The risk-difference estimate is 0.798, its 95% confidence interval is 0.645 to 0.950, and the unadjusted p-value is <0.001. In the posted comparison, recurrence was recorded for 26.0 of 30.0 participants in conservative treatment and 2.0 of 29.0 in mesh. This is a description of the registry’s reported outcome, not a complete assessment of treatment effectiveness or patient benefit.

The Quill suture and mesh event counts were closer: 3.0 of 27.0 and 2.0 of 29.0, respectively. Their risk-difference interval, -0.108 to 0.192, includes zero, and the unadjusted p-value is 0.58. These data do not provide a precise estimate of the difference between those surgical approaches. A lack of a statistically clear difference does not demonstrate that the treatments are equivalent; equivalence would require a prespecified margin and a suitable analysis, neither of which is reported in the registry record.

The results apply to recurrence as recorded by CT scan or clinical investigation at the specified follow-up. They do not establish what happened after that assessment, the severity of recurrence, or how participants’ symptoms and function changed. The registry lists postoperative pain and adverse events as secondary outcomes, but their results are not reported in the registry record. Thus the posted primary outcome cannot answer the full study question about safety and longer-term results.

Statistical significance is not the same as clinical importance, and an observed association in a trial is not a substitute for considering the study’s design and data quality. The registry does not report key details about eligibility, allocation procedures, outcome handling, missing data, or the analysis plan. The findings are best understood as the reported one-year recurrence comparisons, with uncertainty described by their confidence intervals and limitations in the accompanying registry information.

16. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can yield different levels of precision for different contrasts within the same study. The Quill suture and mesh arms had relatively similar posted recurrence counts, and the resulting risk-difference interval is broad and includes no difference. The conservative-treatment comparison has a much larger observed contrast and an interval that remains above zero. The two comparisons therefore do not support the same degree of statistical certainty, even though they share a reference arm and endpoint.

The example also shows why absolute and relative measures should be read together. The risk difference describes the absolute contrast in event risk, while risk ratios and odds ratios express relative contrasts on different scales. Wide intervals for a relative measure can make its magnitude uncertain even when the point estimate is large. For common outcomes, the odds ratio can look more extreme than the risk ratio, so interpreting it as a direct risk contrast can mislead.

Planning calculations based on observed effects are especially sensitive to the size of the effect chosen for future studies. The Quill comparison’s smaller observed effect leads to much larger illustrative participant requirements than the conservative-treatment comparison. Such calculations are useful for understanding the implications of assumptions, but they do not validate the observed effect as the expected effect in another study. A planning estimate based on an observed effect can be optimistic if that estimate is unstable.

Finally, the registry record demonstrates the importance of reporting details beyond a p-value. Denominators, confidence intervals, analysis populations, missing-data handling, multiplicity decisions, and outcome definitions all shape interpretation. Several of those details are not reported in the registry record. Statistical reading therefore involves both interpreting the posted estimates and recognizing what cannot be resolved from the available record.

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 offers limited detail about the enrolled population. It does not report eligibility criteria, baseline characteristics, recruitment setting, or demographic information, so the applicability of the results to particular patient groups cannot be assessed from the record alone. Although the study is described as randomized and single-masked, the randomization method, concealment procedures, and identity of the masked party are not reported.

The primary outcome is described as recurrence assessed by CT scan or clinical investigation one year after surgery, but the operational definition of recurrence is not given. The record does not explain how imaging and clinical findings were combined, whether assessors were blinded, or how disagreements were resolved. It also does not report whether all participants had outcome assessment or why the reported denominators differ from the arm descriptions.

The posted primary comparisons are unadjusted, and the statistical test or model, confidence-interval method, and analysis population are not reported. There is no registry information about missing-data procedures, adherence to assigned treatments, protocol deviations, interim analyses, or multiplicity adjustment. Results for the listed pain and adverse-event secondary outcomes are not reported in the registry record.

Follow-up for the primary outcome is specified at one year after surgery; the record does not give primary recurrence results beyond that point. The stated sample-size illustrations use observed effects and do not describe the trial’s original design assumptions. These gaps limit assessment of precision, bias, generalizability, longer-term outcomes, and the extent to which the posted estimates match a prespecified analysis.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Study to Evaluate Two Different Surgical Methods for Treatment for Abdominal Wall Diastasis — NCT01586741.
• Registry record last updated 2020-12-23; status last verified 2020-11.
• Results first posted 2020-12-23.
• 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

NCT01586741 is a completed, prospective randomized, parallel-group study sponsored by Karolinska Institutet. It compared polypropylene mesh, double-row absorbable Quill suture, and conservative abdominal exercise for abdominal wall diastasis. Registry enrollment is 96, and the study start and primary completion are recorded as 2009-12 and 2011-11.

The primary outcome was recurrence one year after surgery, assessed by CT scan or clinical investigation. The mesh and Quill arms had 2.0 of 29.0 and 3.0 of 27.0 recorded recurrences; conservative treatment had 26.0 of 30.0. The Quill-versus-mesh risk difference was 0.042, with a 95% confidence interval from -0.108 to 0.192 and an unadjusted p-value of 0.58. The conservative-treatment-versus-mesh risk difference was 0.798, with a 95% confidence interval from 0.645 to 0.950 and an unadjusted p-value of <0.001.

Zero serious adverse events, other adverse events, and deaths are reported in each arm. Results for the listed secondary outcomes are not reported in the registry record.