Prevention of Peritonitis in Peritoneal Dialysis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prevention of Peritonitis in Peritoneal Dialysis (NCT01293799), a randomized na study. The primary outcome is Time to the First Dialysis-associated Peritonitis Episode in the Retraining Group and the Control Group.

2. Clinical Question

The clinical rationale in the registry is that peritonitis is an important problem during peritoneal dialysis and that reinforcing knowledge and practical ability might reduce its occurrence. The trial therefore tested a structured follow-up and retraining approach against the centers’ usual routines. Its primary outcome concerns the timing of a first episode, rather than only whether any episode occurred over a fixed period. The registry describes follow-up from one month after peritoneal-dialysis start, when randomization occurred, up to a maximum of 36 months after treatment start. These details define the population, care strategies, and event being compared; they do not by themselves establish that one strategy is better.

3. Trial Design

This was a randomized, parallel-group trial with no masking. The registry lists the phase as not applicable and the status as completed. Sahlgrenska University Hospital is named as sponsor. The posted enrollment is 713. The primary-outcome population description says 671 new peritoneal-dialysis patients were randomized; the registry’s summary describes an objective to include 750 patients. These are distinct record figures, and the registry does not explain the difference between them.

Eligible primary-outcome participants were adults aged 18 years or older, peritonitis-free, starting peritoneal dialysis, and able to perform it without assistance. The retraining group was tested at regular intervals after dialysis began and after each peritonitis episode, with a focus on infection prophylaxis. Retraining was given when needed until test goals were reached. The control group followed clinic routines. The record describes the study as multicenter and lists Denmark, Norway, Sweden, Finland, Estonia, Latvia, the Netherlands, and the United Kingdom as participating countries.

The registry gives a start date of 2010-01 and primary completion of 2012-12. Its summary states that the study would go on for 6 years, while the primary outcome timeframe specifies observation from one month after dialysis start through a maximum of 36 months after start, or maximally 35 months after randomization. The record does not explain the relationship between these durations. The primary analysis handled participants who stopped peritoneal dialysis for reasons other than peritonitis according to the intention-to-treat principle. Other details of the trial’s analysis populations and handling of missing outcome information are 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: A number of 671 new patients with peritoneal dialysis (PD), peritonitis-free, aged 18 years or more, and able to perform PD without assistance were randomized to a control group and a retraining group. Participant who stopped PD treatment due to causes other than peritonitis were managed according to the intention-to-treat principle.

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 Time to the First Dialysis-associated Peritonitis Episode in the Retraining Group and the Control Group, measured over Participants were followed from 1 month after PD start (time of randomization) up to a maximum of 36 months after start of peritoneal dialysis, i.e. to maximally 35 months after randomization. Time to first peritonitis was calculated for each participant..

The primary endpoint is time, measured in days from randomization to the first peritonitis episode. It is a time-to-event outcome: it uses both whether an event occurred during follow-up and how long participants remained without a recorded event. The reported group summaries are medians, accompanied by interquartile ranges. The median time was 381 days in the retraining group, with an interquartile range of 154 to 555, and 368 days in the control group, with an interquartile range of 161 to 617.

Time-to-event methods are useful when participants may have different follow-up durations or may end observation without experiencing the event. The registry describes estimation of peritonitis-free survival curves and a comparison of those curves, as well as calculation of an unadjusted hazard ratio using a Cox regression model. Participants who stopped dialysis for causes other than peritonitis were managed according to the intention-to-treat principle. Further detail on how that principle was implemented for the time-to-event analysis is not reported in the registry record.

The primary endpoint addresses the timing of a first episode; it does not count the full burden of repeated episodes. The registry separately reports secondary outcomes for first and all peritonitis episodes. The endpoint’s interpretation depends on the comparison of the full time-to-event experience, not solely on comparing the two medians. A hazard ratio summarizes the relative event hazard over follow-up under the model, while a confidence interval expresses uncertainty around that estimate. Neither statistic alone describes every participant’s experience or establishes a causal mechanism.

7. Results Posted in the Registry

• The Retraining Group vs Control Group: hazard ratio 0.92 (95% CI 0.71–1.19), reported p = 0.510 (as reported in the registry).

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.

Incidence of a First Dialysis-associated Peritonitis Episode in the Control and the Retraining Group

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • The Retraining Group: 0.29 versus 0.31 (Peritonitis events per patient-year) on control; rate ratio 0.94 (95% CI 0.71–1.23, derived from the posted confidence limits); p ≈ 0.634.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between The Retraining Group and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of All Peritonitis Episodes in the Control Group and the Retraining Group

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • The Retraining Group: 0.33 versus 0.36 (Peritonitis event rate per patient year) on control; rate ratio 0.92 (95% CI 0.74–1.14, derived from the posted confidence limits); p ≈ 0.431.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between The Retraining Group and the control. The interval gives the range of effects that remain compatible with the data.

Across the two secondary outcomes, the overall pattern is compatible with the primary result: the estimates lean toward fewer peritonitis events with retraining, but the inferential uncertainty does not clearly separate the groups. The outcomes add context by considering both a first episode and all episodes, while the primary endpoint focuses on time until a first episode. Together, they provide related but non-identical views of the event experience.

Secondary analyses generally deserve less weight than the designated primary outcome when assessing the trial’s central question. They may involve multiple outcomes, and examining more comparisons increases the chance of finding an apparently notable result by chance. Whether and how the trial adjusted for multiplicity is not reported in the registry record. The registry lists two secondary outcomes, but it does not report a complete hierarchy of hypotheses or a prespecified multiplicity procedure.

The secondary outcomes should therefore be read as supportive context rather than as independent confirmation of a treatment effect. Their broadly similar direction does not remove the uncertainty in the primary estimate, and their different measurement scales mean that they cannot be combined informally into a single effect. The record does not report a composite analysis or an adjusted overall estimate across these endpoints.

Because the secondary results are not a substitute for the primary analysis, their interpretation should consider both the prespecified status of each outcome and the number of statistical comparisons made. The record does not give enough information to determine the full set of analyses considered or whether additional outcomes were planned but not posted. Consequently, the pattern across the posted secondary endpoints is informative but should not be treated as definitive evidence on its own.

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

• Incidence of a First Dialysis-associated Peritonitis Episode in the Control and the Retraining Group
• Incidence of All Peritonitis Episodes in the Control Group and the Retraining Group

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time to first peritonitis, so the reported analysis uses methods for time-to-event data. In general, such methods account for the timing of an event and allow participants to contribute observed follow-up even if they do not experience the event during that period. The registry states that cumulative time without peritonitis was analyzed using a Cox regression model, from which an unadjusted hazard ratio was calculated. It also states that Kaplan–Meier methods were used to estimate peritonitis-free survival curves and that a log-rank test was used to compare the curves.

What the hazard ratio describes

In general, a hazard is the instantaneous event rate among participants who have not yet experienced the event, conditional on remaining under observation and event-free up to that time. A hazard ratio compares the hazards between groups over follow-up. A value of 1 is the no-difference reference; values below or above 1 indicate the direction of the estimated comparison, according to the group order. The registry reports 0.92 for retraining compared with control. A hazard ratio is not a ratio of the group medians, and it is not the probability that a participant will have peritonitis. Interpreting one hazard ratio across time also depends on the proportional-hazards structure of the Cox model. Whether that assumption was assessed is not reported in the registry record.

Kaplan–Meier estimates and the log-rank test

In general, the Kaplan–Meier method estimates the probability of remaining event-free over time while accounting for participants whose event status becomes unobserved before the end of follow-up. A survival curve can display how the event-free proportion changes throughout follow-up rather than reducing the comparison to a single summary time. The log-rank test assesses whether the observed event-time patterns differ between groups. The registry reports a log-rank p-value of 0.51. A p-value measures how compatible the observed data are with a specified no-difference hypothesis under the test’s assumptions; it is not the probability that the hypothesis is true, nor does it quantify the size of an effect.

The primary group summaries are medians with interquartile ranges. A median time is a distributional summary, while the hazard ratio and log-rank test use the event-time information across follow-up. These measures answer related but not identical questions, which is why the medians alone should not replace the reported time-to-event comparison.

Secondary event-rate analyses

The secondary outcomes summarize peritonitis episodes relative to participant time. The sponsor reports generalized linear methods and risk ratios for both secondary outcomes. The registry does not provide additional detail about the fitted models or their covariates. The separate recalculations of rates use the posted group summaries and a Poisson approach, with rate ratios and confidence intervals. In general, a rate ratio compares events per unit of person-time, whereas a risk ratio compares risks over a specified period. Those measures need not be numerically identical because they summarize the data on different scales and may reflect different analysis specifications.

For the recalculated secondary estimates, the confidence intervals are based on the posted rate summaries. These are simple, unadjusted recalculations and should be distinguished from the sponsor’s reported analyses. The registry record reports no discrepancy flag for the sponsor and recalculated results. The sponsor’s own analysis remains the trial’s reported analysis; the recalculations are supplementary summaries, not replacements for it. Generalized linear methods can accommodate outcome distributions and link functions chosen for the analysis, but the exact model specification is not reported in the registry record.

Confidence intervals and evidence

In general, a confidence interval describes the range of estimates reasonably compatible with the data and the method, at the stated confidence level. The primary 95% confidence interval is 0.71 to 1.19. Because it includes the no-difference value of 1, it does not rule out either direction of effect. The reported p-value and confidence interval convey related evidence, though they are not interchangeable: the interval emphasizes uncertainty about effect size, while the p-value measures compatibility with a particular null hypothesis.

All inferential statistics depend on assumptions about how observations were collected and analyzed. For time-to-event analyses, handling of censoring and model assumptions matters; for event rates, the chosen distributional model and person-time calculation matter. The registry describes the broad methods but does not report all diagnostics or detailed specifications. The results should therefore be read as the sponsor-reported estimates within the scope of the available description, not as a complete account of every analytic decision.

11. Confidence Intervals and Precision

The primary hazard-ratio estimate is 0.92, with a 95% confidence interval from 0.71 to 1.19. This interval spans the no-difference reference value of 1 and includes estimates on either side. The point estimate alone suggests a lower hazard in the retraining group, but the confidence interval shows that the direction and size of the underlying difference remain uncertain. The p-value of 0.51 is consistent with that uncertainty; it does not establish that the groups are identical.

In general, a confidence interval is a measure of statistical precision: narrower intervals indicate that the data constrain the estimate more tightly, while wider intervals leave a broader range of plausible effects. Precision is not the same as importance. A narrow interval can still include effects that matter, and a point estimate that appears favorable can be imprecise. Clinical importance cannot be determined from a p-value alone, and the registry does not specify a threshold for a clinically important difference.

The secondary event-rate summaries also have confidence intervals that include their no-difference references. Their precision is limited enough that the estimates do not clearly distinguish a reduction from little difference or an increase. Those rate estimates use a different outcome scale from the primary hazard ratio, so their interval widths should not be compared as though they measured the same quantity.

The registry does not report the number of primary events supporting the hazard ratio or detailed information on censoring. Those omissions limit a fuller assessment of the information underlying the confidence interval. The interval should therefore be read as the uncertainty conveyed by the reported analysis, not as a guarantee that all plausible sources of uncertainty have been captured.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the original design justification for the trial. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

For the primary time-to-event outcome, the planning figures are total numbers of events, not participants per arm. For the secondary event-rate outcomes, the figures are participants per arm. The distinction matters: a total-event target is an event-count requirement across the comparison, whereas a per-arm figure is a participant count for each group. The table’s labels specify which interpretation applies to each outcome.

The 80% power column describes the planned chance of detecting the chosen effect under the stated assumptions if that effect is present. The 90% power column uses a higher target chance of detection under those same assumptions. These are design-planning quantities; they do not state the chance that the trial’s conclusion is correct. This is not observed power.

Each row considers a different fraction of the observed effect. The smaller the effect the study aims to detect, the more information is generally needed, so the planning figures increase as the target effect becomes smaller. The displayed counts are illustrations based on the observed estimates and the stated assumptions, not a retrospective claim that the trial should necessarily have enrolled those counts. In particular, the primary figures refer to events rather than a total participant enrollment, and actual event accrual depends on event occurrence and follow-up. The registry’s posted enrollment is not itself the same quantity as these planning targets.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.920, so ln(HR) = -0.0834.
2. d = 4 × (1.96 + 0.842)² / [ln(0.920)]² = 4,515.7, rounded up to 4,516 events in total 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
hr <- 0.92                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(1293799)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 4,516 (80% power), 6,046 (90% power)
 75% of observed effect: events = 8,028 (80% power), 10,748 (90% power)
 50% of observed effect: events = 18,063 (80% power), 24,182 (90% power)
Simulated power with 4,516 events: 0.800 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 7,602 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 713 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 12.0986301369863          # control-arm median, months (converted from the posted unit)
hr          <- 0.92          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
     Analysis               Value Efficacy
    IA 1: 33%                   Z   3.7103
      N: 5802         p (1-sided)   0.0001
 Events: 2039        ~HR at bound   0.8484
    Month: 18    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.92   0.0338
    IA 2: 67%                   Z   2.5114
      N: 7602         p (1-sided)   0.0060
 Events: 4077        ~HR at bound   0.9243
    Month: 29    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.92   0.5603
        Final                   Z   1.9930
      N: 7602         p (1-sided)   0.0231
 Events: 6116        ~HR at bound   0.9503
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.92   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The sponsor’s primary analysis reports a hazard ratio of 0.92, a 95% confidence interval from 0.71 to 1.19, and a log-rank p-value of 0.51. These are the registry’s reported inferential results for the primary time-to-first-peritonitis comparison. The primary outcome summaries also give the group medians and interquartile ranges, but the sponsor’s principal comparison is the time-to-event analysis rather than a test of the two medians alone.

For the secondary outcomes, the sponsor reports generalized linear methods and risk ratios. The additional rate-ratio estimates are unadjusted recalculations from posted summary statistics using a Poisson approach. They are useful as supplementary checks of the event-rate pattern, but they are not the sponsor’s fitted analyses and may differ because the measures and analytic methods are not identical. The sponsor’s analyses and the recalculations point to a similar broad pattern of uncertainty; no discrepancy is flagged in the registry record.

The recalculations do not revise the registry’s reported results. They are not adjusted for any factors beyond the posted summaries and do not add information that was absent from the original record. Where reported and recalculated results differ in a given setting, the sponsor’s own analysis takes precedence when the record identifies a discrepancy. The available record does not provide enough model detail to explain every aspect of the sponsor’s secondary analyses.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses or outcomes are tested: even if none represents a real group difference, the chance of at least one apparently unusual result can increase as more tests are performed. The registry lists two secondary peritonitis outcomes in addition to the primary outcome. It does not report a multiplicity adjustment, a testing hierarchy, or whether the secondary tests were intended to be confirmatory or exploratory. These details are not reported in the registry record, so the secondary p-values should not be interpreted as if a multiplicity strategy were known.

The record reports the primary analysis population and says that participants who stopped peritoneal dialysis due to causes other than peritonitis were managed according to the intention-to-treat principle. It does not fully describe the analysis population for each secondary outcome, the treatment of missing observations, or the handling of participants with incomplete follow-up. Although time-to-event methods commonly accommodate censoring, the precise censoring rules and their implementation are not reported in the registry record.

The primary-outcome description includes 671 randomized participants, while posted enrollment is 713 and the study summary states an objective of 750 participants. The registry does not explain the relationship between those counts, such as whether they reflect different stages or definitions of enrollment. It also does not provide a participant-flow account or reasons for non-inclusion in the primary outcome analysis. These omissions make it difficult to assess how the analyzed population relates to all enrolled participants.

The registry describes the trial’s primary methods at a broad level but does not provide a full statistical analysis plan, the original sample-size justification, interim-analysis plans, or a detailed account of all outcome analyses. Such information would help clarify which tests were planned in advance, how missing data were addressed, and how secondary findings should be weighted. In its absence, interpretation should remain close to the explicitly reported analysis and avoid assumptions about procedures that are not documented.

17. 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’s safety summary lists a group called the Follow-up Group and a Control Group. It reports 340 participants at risk in the Follow-up Group and 331 in control. For both groups, the count affected by serious adverse events is 0, and the count affected by other adverse events is also 0. The registry lists 27 deaths in the Follow-up Group and 29 in control.

These figures are counts, not rates, and the record does not provide a safety follow-up duration or additional detail about event definitions, causes of death, or how events were collected. The safety group label Follow-up Group is not identical to the intervention label used for the primary outcome, so the record does not clarify whether it refers to the same retraining group. No serious adverse-event terms are listed. The zero counts should be understood as the posted registry summaries, not as proof that no events of any kind occurred or that the groups had identical safety experience.

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

The result describes a randomized comparison of regular skills testing and retraining with routine clinic follow-up among adults starting peritoneal dialysis who could perform it without assistance. For the primary endpoint, the estimated hazard ratio is close to the no-difference reference, and its confidence interval includes values on both sides of that reference. The analysis therefore does not provide clear evidence of a difference in time to first peritonitis, while also leaving uncertainty about the size and direction of any underlying difference.

This finding does not establish that retraining and clinic routine are equivalent. Equivalence requires a defined margin and an analysis designed to assess whether the difference lies within that margin; neither is reported. It also does not establish that retraining has no effect. A result that does not provide strong evidence against no difference can reflect genuine similarity, limited precision, or both. The interval is essential to understanding what the data can and cannot distinguish.

The secondary endpoints add information about rates of first and repeated peritonitis episodes, but they do not resolve the primary uncertainty. The registry record does not give enough detail about multiplicity, missing data, or all analysis choices to support broader claims beyond the posted comparisons. Nor does the primary outcome alone establish effects on technique failure, hospital days, mortality, or quality of life; although some of these were mentioned in the study objective, corresponding results are not reported in the record summarized for these outcomes.

The findings apply to the population and follow-up described in the registry, and the record does not establish whether they generalize to people requiring assistance with peritoneal dialysis or to different care settings. The trial compares a structured retraining approach with local clinic routines, which may vary by center. The result should therefore be interpreted as an estimate from this particular randomized comparison, with the stated limits of its reporting, rather than as a universal conclusion about all retraining programs or all dialysis populations.

19. Why This Trial Matters Statistically

This trial is statistically informative because it compares a behavioral and educational strategy using a clinically relevant time-to-event outcome. Its design illustrates why a randomized comparison and a prespecified primary endpoint matter: a plausible rationale for retraining is not itself evidence that event timing differs, and the analysis must quantify both the estimated effect and its uncertainty.

The result also shows why a point estimate and a p-value are insufficient on their own. The hazard-ratio estimate lies below the no-difference value, but the confidence interval spans both directions. Readers can see that the point estimate is not a precise verdict. This is a central biostatistical distinction: lack of strong evidence for a difference is not proof of no effect, just as a favorable-looking estimate is not proof of benefit.

The trial also highlights the difference between outcomes. Time to a first episode, incidence of first episodes, and rate of all episodes represent distinct summaries. They can offer complementary perspectives, but should not be casually substituted for each other or combined without a defined analysis plan. The relationship between the primary result and secondary endpoints is best understood as a pattern of estimates with uncertainty, not as a vote among outcomes.

Finally, the record illustrates the importance of transparent reporting. The difference among posted enrollment, the stated objective, and the primary population count, along with missing detail on original planning, multiplicity, missing data, and analysis populations, constrains interpretation. Reporting these design and analysis details alongside estimates and confidence intervals would allow readers to judge precision, bias risks, and the strength of secondary evidence more fully.

20. 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 limitations follow from the record’s level of detail. The primary population count is 671, posted enrollment is 713, and the study summary gives an objective of 750 participants. The registry does not reconcile those figures or provide a participant-flow description. Without that information, readers cannot determine from the record alone how many enrolled participants contributed to each outcome analysis or why any were not included.

The primary analysis description names Cox regression, Kaplan–Meier estimation, and a log-rank comparison, but does not report diagnostics or detailed model specifications. Assessment of proportional hazards, censoring rules, center effects, and any adjustment variables is not reported in the registry record. It also does not provide the number of primary events, which limits appraisal of the amount of event information underlying the estimate.

The intervention was compared with clinic routines, and the record does not describe whether those routines were standardized across centers or how consistently retraining was delivered. Masking was none, as recorded. The registry does not describe adherence to testing or retraining, contamination between groups, or fidelity to the assigned strategies. These issues could affect how closely the comparison represents the intended contrast, but their extent cannot be determined from the record.

Further limitations are the absence of a detailed statistical analysis plan, the trial’s original sample-size justification, interim-analysis information, and a stated approach to multiplicity. The record also does not report detailed missing-data handling or the full set of analysis populations. Finally, the available summary does not provide results for every outcome mentioned in the study objective, such as technique failure or hospitalization days due to peritonitis. Conclusions should be confined to the posted outcomes and analyses.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Prevention of Peritonitis in Peritoneal Dialysis — NCT01293799.
• Registry record last updated 2025-12-16; status last verified 2025-11.
• Results first posted 2025-12-16.
• 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.

24. Record Summary

The registry record describes a completed, randomized, parallel-group, unmasked trial sponsored by Sahlgrenska University Hospital. It compares regular peritoneal-dialysis skills testing and retraining with clinic routine among adults able to perform dialysis without assistance. The primary outcome is time from randomization to a first peritonitis episode, analyzed using time-to-event methods. The reported hazard ratio is 0.92, with a 95% confidence interval from 0.71 to 1.19 and a log-rank p-value of 0.51.

The secondary outcomes concern first and all peritonitis episodes. Their overall pattern is compatible with uncertainty about a group difference. The record reports enrollment of 713, a primary population of 671, and a study objective of 750; it does not explain the differences. Details about original sample-size planning, multiplicity, missing data, interim analyses, and several analysis specifications are not reported in the registry record. The primary estimate should be interpreted with its confidence interval and these reporting limitations in view.