Vancomycin Plus Moxifloxacin Versus Vancomycin Plus Ceftazidime for the Treatment of Peritoneal Dialysis (PD)-Related Peritonitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Vancomycin Plus Moxifloxacin Versus Vancomycin Plus Ceftazidime for the Treatment of Peritoneal Dialysis (PD)-Related Peritonitis (NCT02787057), a randomized na study. The primary outcome is Complete Cure Rate.

2. Clinical Question

The registry describes a pilot randomized controlled study of two antibiotic regimens. Its stated rationale contrasts oral administration of a quinolone, described as potentially more convenient and economical, with a conventional combination of intraperitoneal antibiotics. The primary outcome focuses on complete cure rather than an isolated early response: it incorporates resolution of clinical and dialysate findings as well as the absence of relapse within 4 weeks after therapy ends.

The comparison is between treatment strategies as described in the registry, not between moxifloxacin and ceftazidime given alone. Both groups received intraperitoneal vancomycin; the accompanying antibiotic and its route differed. This distinction matters when interpreting the estimate: it describes the difference between the two combinations, not the separate effect of any single drug. The registry record does not report further eligibility criteria or participant characteristics.

3. Trial Design

This was a randomized, single-masked, parallel-group pilot study. The registry reports enrollment of 80 participants and a completed status. It identifies Peking University First Hospital as the sponsor. The listed start was 2012-11, and primary completion was 2016-04. The trial phase is listed as NA.

Participants were assigned to one of two regimens. The control group received intraperitoneal vancomycin 1g every 5 days with intraperitoneal ceftazidime 1g QD. The study group received the same stated vancomycin schedule with oral moxifloxacin 400mg QD. For both groups, duration was described as based on ISPD guideline recommendations. The registry does not report the specific masking procedures, such as which participants or study personnel were masked.

The primary outcome was complete cure rate, recorded as a count of participants and assessed within 4 weeks of completion of therapy. The posted primary outcome counts are based on 40 participants per group. Three secondary outcomes are also posted: primary response rate on day 10, primary treatment failure after 3 days, and secondary treatment failure after 6 to 8 days. Each is reported as a participant count for both groups.

The registry classifies this as a pilot randomized controlled study, but the original sample-size justification and planned analysis methods are not reported in the registry record. The record also does not report an analysis population, details about allocation concealment, protocol deviations, or whether outcomes were assessed by masked evaluators. These omissions limit how much can be inferred about the implementation and analysis of the randomized comparison.

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 Complete Cure Rate, measured over within 4 weeks of completion of therapy.

The primary endpoint is complete cure rate, measured as the number of participants meeting the registry’s definition of complete cure within 4 weeks of completing therapy. The definition requires complete resolution of peritonitis using antibiotics alone, followed by no relapse during the specified follow-up window. Resolution includes normalization of body temperature, resolution of abdominal pain, clearing of dialysate, and a PD effluent neutrophil count less than 100 cells/mL with the proportion of polynuclear cells less than 50%.

This endpoint combines clinical and dialysate findings with a period free of relapse. It therefore captures more than an early improvement while participants are receiving treatment. The registry’s definition also makes clear that cure is assessed without requiring an additional treatment beyond antibiotics alone. The posted outcome is a count in each group; the comparison estimates the difference in the probability of meeting the full definition between the study and control regimens.

In general, a composite clinical definition can summarize several related conditions into one endpoint, but interpretation depends on the components and timing specified. In this trial, the required components are explicitly described in the registry, along with the post-therapy window for relapse. The record does not report whether the individual components were analyzed separately or how disagreements in endpoint assessment were handled.

7. Results Posted in the Registry

• Study Group: 77.5% (31/40) versus 80.0% (32/40) on control; risk difference -2.5 percentage points (95% CI -20.4 to 15.4), risk ratio 0.97 (0.77–1.22); unadjusted two-proportion z-test p = 0.785.

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.

Primary Response Rate

• 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:
  • Study Group: 67.5% (27/40) versus 80.0% (32/40) on control; risk difference -12.5 percentage points (95% CI -31.6 to 6.6), risk ratio 0.84 (0.65–1.10); unadjusted two-proportion z-test p = 0.204.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Study Group and the control. The interval gives the range of effects that remain compatible with the data.

Primary Treatment Failure Rate

• 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:
  • Study Group: 32.5% (13/40) versus 20.0% (8/40) on control; risk difference 12.5 percentage points (95% CI -6.6 to 31.6), risk ratio 1.62 (0.76–3.49); unadjusted two-proportion z-test p = 0.204.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Study Group and the control. The interval gives the range of effects that remain compatible with the data.

Secondary Treatment Failure Rate

• 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:
  • Study Group: 10.0% (4/40) versus 12.5% (5/40) on control; risk difference -2.5 percentage points (95% CI -16.3 to 11.3), risk ratio 0.80 (0.23–2.76); unadjusted two-proportion z-test p = 0.723.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Study Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes describe response and treatment failure at different stages: response on day 10, primary treatment failure after 3 days, and secondary treatment failure after 6 to 8 days. Across these measures, the point estimates are mixed rather than forming a consistent pattern favoring one combination. The early response and early failure estimates lean in the control group’s direction, while the later failure estimate is close to no difference. Their intervals include no difference, so the posted comparisons do not provide precise evidence of distinct group effects.

This pattern does not contradict the primary result so much as provide a separate view of treatment course at other timepoints. The primary endpoint is a complete cure definition assessed within 4 weeks after therapy completion; an early response or failure is not the same outcome and does not by itself determine whether a participant eventually met the cure definition. The secondary measures should therefore be interpreted as complementary descriptions, not substitutes for the primary endpoint.

Unadjusted secondary results carry less weight as confirmatory evidence when several outcomes are examined. In general, testing multiple outcomes creates more opportunities for apparently notable findings to arise by chance. A multiplicity procedure can address that issue, but no such plan is reported in the registry record. The secondary results are best treated as exploratory context for the primary comparison, especially because the study is designated a pilot and the estimates are imprecise.

The registry does not report whether these outcomes were prespecified in a protocol, how missing measurements were handled, or whether any secondary outcome had a formal role in the study’s conclusions. The posted data support describing the direction and uncertainty of each comparison, but not choosing one secondary result as decisive evidence.

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

• Primary Response Rate
• Primary Treatment Failure Rate
• Secondary Treatment Failure Rate

9. Statistical Interpretation

10. Statistical Methods Explained

The posted comparisons use binary outcomes: each participant either met the defined outcome or did not. For the primary endpoint, the registry reports the number of participants meeting the cure definition and the number assessed in each group. A risk difference expresses the difference in outcome probability between groups. The comparison is oriented as study group minus control group, so a negative estimate indicates a lower observed outcome probability in the study group, and a positive estimate indicates a higher observed probability. This direction describes the data; it does not establish a causal explanation for the difference.

What does a risk difference communicate?

In general, a risk difference gives an absolute contrast on the probability scale, rather than a relative comparison. A value of zero represents no difference in probability between groups. For the primary endpoint, the estimate is -0.025. Its confidence interval extends from -0.204 to 0.154, so it includes zero and includes estimates in either direction. The unadjusted p-value is 0.785. Taken together, these statistics do not provide strong evidence of a difference, but they also do not tightly constrain the possible size or direction of the difference.

The registry also posts risk ratios and odds ratios. In general, a risk ratio compares the outcome probabilities in the two groups, while an odds ratio compares their odds. The no-difference reference value for each ratio is one. For the primary result, the posted intervals for both measures include that reference value. These relative measures answer a different mathematical question from the risk difference. They can be harder to interpret clinically, particularly when outcome counts are limited, so the absolute risk difference is useful alongside them.

How should the p-value be read?

In general, a p-value is calculated under a statistical model that assumes no difference between groups and describes how unusual results at least as discrepant as the observed data would be under that model. It is not the probability that the null hypothesis is true, nor does it quantify the probability that the result will replicate. The registry posts unadjusted p-values for the comparisons. It does not report whether an adjustment or alternative inferential procedure was prespecified.

Random assignment is intended to make groups comparable on average, including on measured and unmeasured characteristics. In a particular trial, however, chance differences can remain. The registry record does not report baseline characteristics or the methods used to generate or conceal the allocation sequence, so those aspects of implementation cannot be evaluated from the posted information.

Why is the pilot designation relevant?

The study is described as a pilot randomized controlled study. A pilot can provide experience with recruitment, treatment delivery, outcome measurement, and the variability of an estimate. The registry does not state the role intended for this pilot or report its original sample-size justification. Thus, the label alone does not establish which decisions the study was designed to inform. The observed enrollment and uncertainty interval are more relevant when judging the precision of the posted primary estimate.

In general, over-dispersion is relevant when observed variability is greater than a statistical model expects. Such extra variability can make model-based standard errors too small and intervals too narrow if it is not accounted for. The posted outcomes are participant counts, not a continuous or count-rate measure with a reported dispersion parameter. The registry does not describe an over-dispersion model, and there is no reported basis for attributing the uncertainty in these binary comparisons to over-dispersion.

The record lists zero reported analyses for the primary comparison and no reported analyses for the secondary outcomes, even though summary outcome counts and unadjusted comparisons are posted. It does not describe the statistical software, confidence-interval method, handling of missing data, analysis population, covariate adjustment, or any interim analysis. Those procedures are not reported in the registry record, so the posted estimates should be interpreted as the summaries and unadjusted comparisons recorded, without assuming additional analysis choices.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.025, with a 95% confidence interval from -0.204 to 0.154. In general, a confidence interval is a range of values reasonably compatible with the observed data under the method’s assumptions. It reflects uncertainty in the estimate; it is not a range containing a fixed proportion of individual participant outcomes, and it does not assign a probability to the true effect after the data have been observed.

The interval includes zero, which represents no difference on the risk-difference scale. It also extends to both a negative and a positive difference. That breadth means the data are compatible with possibilities favoring either group, as well as with little difference. The point estimate is near zero, but the interval shows that the estimate is not precise enough to rule out appreciable differences in either direction.

The ratio measures likewise have intervals that extend across their no-difference reference value of one. This is consistent with the uncertainty conveyed by the risk-difference interval. No single statistic should be read in isolation: the point estimate indicates the direction and size of the observed contrast, the interval conveys precision, and the unadjusted p-value describes compatibility with a no-difference model under its assumptions.

The registry does not report a clinically acceptable equivalence or noninferiority margin. Without such a prespecified threshold, the interval cannot be used to establish that the regimens are sufficiently similar. The appropriate reading is that the posted estimate is uncertain and that the available data leave a wide range of contrasts plausible.

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 a report of the trial’s original design calculation. For these binary outcomes, the figures are participants per arm, not total events. The listed 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 80% power column gives the planned number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column uses the same idea but targets a 90% chance. These are design targets, not guarantees about the outcome of a future study. The sample-size illustrations are not observed power.

Rows for 100% of the observed effect use the full observed difference as the planning target. Rows for 75% and 50% of the observed effect use smaller targets. Smaller effects are harder to distinguish from random variation, so they require more participants under the stated assumptions. For the primary cure outcome, the displayed planning counts increase as the assumed fraction of the observed effect decreases. These figures can therefore help readers see how strongly a proposed design depends on the effect size chosen for planning.

The registry’s own original sample-size assumptions and justification are not reported in the registry record. These illustrations should not be mistaken for the rationale behind enrollment of 80 participants in the pilot study. They also do not account for any design features beyond the listed assumptions, such as adjustment, missing outcomes, or departures from the normal approximation.

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 = 0.800; treatment proportion p₁ = 0.775; average p̄ = 0.788.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5785 = 1.1339.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5783 = 0.4867.
4. n = (1.1339 + 0.4867)² / (-0.0250)² = 4,201.9, rounded up to 4,202 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 <- 0.8                          # control proportion
p1 <- 0.775                          # 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(2787057)
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 = 4,202 (80% power), 5,625 (90% power)
 75% of observed effect: n per arm = 7,391 (80% power), 9,893 (90% power)
 50% of observed effect: n per arm = 16,447 (80% power), 22,017 (90% power)
power.prop.test: 4201.9 
Simulated power at n = 4,202 per arm: 0.803 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and three secondary outcomes, with unadjusted comparisons posted for each. It does not report a multiplicity plan, such as a hierarchy of hypotheses or an adjustment across outcomes. In general, when several outcomes are tested, the chance of at least one apparently unusual result can rise. For that reason, secondary comparisons without a reported multiplicity strategy are more appropriately considered exploratory than confirmatory. The primary endpoint remains the clearest registered focus, although the registry does not report a complete statistical analysis plan.

Missing-data handling is not reported in the registry record. The posted counts show 40 participants in each group for the primary and secondary outcomes, but the record does not explain whether these denominators represent all randomized participants, all treated participants, or participants with available measurements. It also does not state how withdrawals, incomplete assessments, or participants with uncertain outcome status were handled. Equal posted denominators alone do not establish that there were no missing data or exclusions.

The analysis population is not reported. In particular, the registry does not specify whether participants were analyzed according to randomized assignment, treatment received, or another rule. It also does not report protocol deviations, crossovers, or adherence. These details matter because excluding participants or regrouping them after randomization can affect the balance created by random assignment.

The registry record does not report an interim analysis or stopping rule, nor does it describe covariate adjustment or a method for dealing with multiple comparisons. These absent details should not be inferred from the posted estimates. As a result, interpretation is limited to the outcome counts and unadjusted comparisons recorded, with the understanding that the trial’s full analysis procedures are not documented in the registry record.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2.5% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event summary reports zero serious adverse events among 40 participants at risk in each group. It also reports one other adverse event among 40 participants at risk in each group. No serious adverse-event terms are listed. The deaths field is not populated with a count, so deaths are not reported in the registry record.

These are event counts in the registry summary, not a complete description of safety. The record does not provide the type, timing, severity, or treatment relatedness of the other adverse events, nor does it describe how events were collected or coded. A count of zero reported serious events should therefore be read as the posted registry figure, not as proof that no serious event occurred outside the information captured in that summary.

In general, safety interpretation depends on the completeness of event ascertainment, the observation period, and the definitions used. Those details are not reported in the registry record. The small number of participants and the limited adverse-event detail also mean that the posted counts offer only a narrow description of events recorded in this study.

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

The primary outcome counts were similar in the two groups: 32 of 40 participants in the control group and 31 of 40 in the study group met the complete-cure definition. The estimated risk difference is -0.025, with a 95% confidence interval from -0.204 to 0.154 and an unadjusted p-value of 0.785. These data show a small observed difference, but the interval is wide and includes differences favoring either group.

Accordingly, the result does not demonstrate that the regimens are equivalent, and it does not establish that one is superior. A non-significant p-value is not proof of no effect. Equivalence or noninferiority requires a design, margin, and analysis suited to those claims; these are not reported in the registry record. The confidence interval is too broad to support a narrow conclusion about how similar the outcomes may be.

The comparison concerns two combinations that both include intraperitoneal vancomycin and differ in the accompanying antibiotic and route. It cannot isolate the effect of moxifloxacin, ceftazidime, or route independently. The primary endpoint is also specific to the registry’s definition and follow-up window; it should not be generalized to unmeasured outcomes or time periods.

The findings are most useful as a description of this pilot comparison and as an illustration of uncertainty in a small randomized study. They do not by themselves determine a treatment choice or establish how the regimens compare in other populations or settings. Further conclusions would depend on evidence beyond the posted results, including adequately precise studies and fuller reporting of design and analysis procedures.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a point estimate that is close to no difference and a precise demonstration of similarity. The observed primary contrast is small, but its confidence interval spans a broad range in both directions. Looking only at the point estimate or p-value would understate the uncertainty that the interval makes visible.

The pilot designation and enrollment of 80 participants put the findings in context. A pilot can generate an estimate that helps inform later planning, but the registry does not report that this study was designed to establish equivalence or to provide a definitive comparison. The planning illustrations based on the observed effect also show how sample-size needs depend on the effect chosen to detect. They are not evidence that the trial had adequate power for a particular claim.

The endpoint definition is another important statistical feature. Complete cure requires multiple conditions, including no relapse within 4 weeks after therapy completion. This makes the primary outcome more comprehensive than an early response measure, while also making its interpretation dependent on the stated definition and follow-up. The different secondary timepoints add context but do not replace the primary endpoint.

Finally, the record demonstrates why transparent reporting of analysis populations, missing outcomes, multiplicity, masking procedures, and sample-size justification matters. Those details are not reported in the registry record. Without them, readers can interpret the posted counts and unadjusted estimates, but cannot fully assess the planned analysis or all potential sources of bias. The central statistical lesson is to consider design, endpoint meaning, estimate direction, and precision together.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific limitations constrain interpretation. The study is identified as a pilot and reports 80 enrolled participants, with 40 in each group for the posted outcomes. The primary confidence interval is broad, leaving uncertainty about the direction and magnitude of the difference. The registry does not report an equivalence or noninferiority margin, so the study cannot be interpreted as demonstrating that the regimens are equivalent.

The registry labels the trial single-masked but does not identify who was masked or how masking was maintained. It does not describe allocation concealment or the process used to generate the randomized sequence. The record also lacks baseline characteristics, so readers cannot assess the observed balance of participant features from the posted information.

The analysis population, missing-data approach, treatment adherence, protocol deviations, and handling of crossovers are not reported in the registry record. The original sample-size justification and complete statistical analysis plan are also not reported. Although unadjusted comparisons are posted, the record does not describe the confidence-interval method or any planned adjustment for multiple outcomes.

The primary endpoint includes several clinical and dialysate criteria plus a relapse-free period. The registry does not report separate results for those components or how endpoint assessments were adjudicated. Safety reporting is limited to event counts, without event descriptions, timing, relatedness, or a populated death count. These gaps do not change the posted numbers, but they limit assessment of how completely the outcomes and safety events were captured.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Vancomycin Plus Moxifloxacin Versus Vancomycin Plus Ceftazidime for the Treatment of Peritoneal Dialysis (PD)-Related Peritonitis — NCT02787057.
• Registry record last updated 2020-03-26; status last verified 2020-03.
• Results first posted 2020-03-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed, single-masked, parallel randomized pilot study comparing two antibiotic combinations for peritoneal dialysis-related peritonitis. Enrollment was 80. The primary endpoint was complete cure within 4 weeks of therapy completion, defined by resolution of peritonitis using antibiotics alone and no relapse during that period.

Complete cure was recorded in 32 of 40 control-group participants and 31 of 40 study-group participants. The risk difference was -0.025, with a 95% confidence interval from -0.204 to 0.154 and an unadjusted p-value of 0.785. The secondary outcomes address response and treatment failure at earlier timepoints and have unadjusted comparisons. Serious adverse events were reported as zero in each group; one other adverse event was reported in each group.

The registry does not report the original sample-size justification, analysis population, missing-data procedures, multiplicity plan, or several details of trial conduct. The main result is therefore best read as an imprecise estimate from a pilot randomized comparison, not as evidence establishing equivalence or superiority.