Comparison of Laser Lithotripsy With and Without Steerable Ureteroscopic Renal Evacuation (SURE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Laser Lithotripsy With and Without Steerable Ureteroscopic Renal Evacuation (SURE) (NCT04519294), a randomized na study. The primary outcome is Stone Free Rate (SFR) - Zero Fragments.

2. Clinical Question

3. Trial Design

This was a prospective, randomized, parallel-group study comparing SURE with standard ureteroscopy using basketing after laser lithotripsy. The registry lists the study as completed, with enrollment of 132. It records a start date of 2021-06-16 and primary completion on 2023-01-30. The phase is listed as NA. The sponsor is Calyxo, Inc.

The masking entry is NONE. This describes the overall masking designation in the registry; it does not mean that every person involved in outcome assessment knew the treatment assignment. For the primary endpoint, the record specifically says that non-contrast CT images were reviewed by blinded central reviewer(s). That distinction matters because a blinded image review can reduce the influence of knowledge of group assignment on assessment, even when the trial is not recorded as masked overall.

Participants were assigned to one of two arms: SURE or standard ureteroscopy with basketing. The published outcome records list 46 participants in the SURE arm and 55 in the standard arm for the primary endpoint, with the same arm counts used for the two posted secondary outcomes. The registry's overall enrollment is 132. The record does not state why the endpoint counts are lower than enrollment, whether the counts reflect exclusions, incomplete imaging, or another analysis-population rule, or whether the stated primary endpoint population was applied in a particular way to each outcome.

The study's principal outcome was a binary endpoint assessed at 30 days: zero residual fragments on CT. Two additional outcomes were posted for the same timeframe, residual stone volume and percentage reduction in stone volume. No formal analysis results are listed in the registry's analyses entry. Statistical comparisons discussed in the posted results are therefore unadjusted recalculations from the outcome summaries, rather than a reported sponsor analysis. The registry does not report the original statistical plan, sample-size justification, or treatment of interim analyses.

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.

Before assignment: In total, 132 subject were enrolled and treated. Of the subjects, 123 were randomized. Of these subjects, subjects whose study participation was discontinued prior to the 30-Day CT, who had poor CT quality, major protocol deviations, or who had their procedures aborted were not included in the efficacy analysis. A total of 101 subjects qualified for the efficacy analysis.

Overall Study

Analysis population for the primary outcome, as defined in the registry: All patients who met all protocol requirements with no major deviations that compromise the ability to assess primary and secondary endpoints.

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 Stone Free Rate (SFR) - Zero Fragments, measured over 30 Days.

The primary endpoint was stone-free rate, defined as the percentage of subjects with zero residual fragments at 30 days. The assessment used non-contrast CT with 1.25mm slice thickness, and the images were read by blinded central reviewer(s). The registry describes the rate as the number of subjects in each arm meeting the zero-fragment definition divided by the total number of subjects treated in that arm. The stated endpoint population consisted of patients who met all protocol requirements and had no major deviations that compromised endpoint assessment.

A binary endpoint gives each participant one of two classifications for this outcome: meeting or not meeting the zero-fragment definition. This makes the result interpretable as the share of participants in each arm who met the specified imaging criterion. It also makes the endpoint stricter than a measure that allows some residual fragments: a participant with any residual fragment would not meet the stated zero-fragment definition, regardless of residual volume.

Using a scheduled CT assessment and a central review process gives the endpoint a defined timepoint and a standardized imaging basis. Blinded review is relevant because it can limit influence from knowledge of treatment assignment while images are assessed. At the same time, the endpoint answers a specific question about imaging status at 30 days. It does not, on its own, describe residual stone volume, the extent of volume reduction, longer-term outcomes, or every potential benefit and harm. Those are distinct questions, and the registry lists residual stone volume and percentage reduction in stone volume as secondary outcomes.

7. Results Posted in the Registry

• SURE: 47.8% (22/46) versus 49.1% (27/55) on control; risk difference -1.3 percentage points (95% CI -20.8 to 18.3), risk ratio 0.97 (0.65–1.46); unadjusted two-proportion z-test p = 0.899.

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.

Residual Stone Volume (RSV)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • SURE: mean 14.30 versus 70.20 on control; difference -55.90 (95% CI -95.22 to -16.58), standardized effect d = -0.51; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for SURE than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Stone Clearance (% Reduction in Stone Volume)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • SURE: mean 97.10 versus 93.30 on control; difference 3.80 (95% CI 0.34 to 7.26), standardized effect d = 0.41; z-test p = 0.032.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for SURE than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes give two related but distinct views of stone clearance. Residual stone volume measures the amount of stone remaining, while percentage reduction describes change in stone volume. The posted group summaries favor SURE numerically on both measures, but their relationship to the primary outcome is not one-to-one. The primary endpoint requires zero residual fragments, so it draws a threshold between participants with and without any detected fragment. Volume measures retain gradations among participants and can reflect the amount remaining even when the zero-fragment criterion is not met.

This distinction helps explain how secondary measures can show group differences while the primary proportions are similar. A group can have lower average residual volume without a clearly different proportion reaching zero fragments. Conversely, the proportion crossing a strict threshold can change without a large shift in average volume. These outcomes are complementary, not interchangeable, and they should not be collapsed into a single conclusion about the overall comparison.

The secondary p-values are unadjusted. Because more than one outcome was assessed, interpretation should account for the possibility of chance findings across multiple comparisons. The registry record does not state whether the secondary endpoints were ordered in a testing hierarchy, whether a multiplicity adjustment was planned, or whether these results were intended as confirmatory. Without that information, the p-values offer limited support for definitive claims and are best considered alongside the effect estimates, uncertainty, endpoint definitions, and any prespecified analysis plan.

The registry lists two secondary outcomes and no reported analyses. It does not report distributional diagnostics, sensitivity analyses, or the handling of incomplete measurements for these outcomes. A particularly spread-out continuous outcome may be sensitive to the distribution of a small number of observations; a mean difference can then summarize the data incompletely. The means, standard deviations, and intervals remain useful descriptive and comparative summaries, but they do not reveal every feature of the participant-level distributions.

Thus, the secondary outcomes add information about volume-based clearance that is not captured by the binary primary endpoint. They make the outcome pattern more informative, while also introducing more interpretive uncertainty because of multiplicity and limited reporting of the analysis methods. They should neither override the primary result nor be ignored; their evidentiary role depends on whether they were prespecified, how missing data were handled, and whether appropriate adjustment was used, none of which is reported in the registry record.

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

• Residual Stone Volume (RSV)
• Stone Clearance (% Reduction in Stone Volume)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a randomized parallel-group comparison and outcome summaries for one binary endpoint and two continuous endpoints. The comparisons discussed in the posted results are unadjusted recalculations from the arm-level summaries. The registry lists no analyses in its reported analyses entry. The original statistical methods, including any prespecified models, covariate adjustments, or analysis hierarchy, are not reported in the registry record.

How is a binary outcome compared?

The primary endpoint classifies participants according to whether they had zero residual fragments at 30 days. The reported arm percentages are 48.0% for SURE and 49.0% for standard ureteroscopy with basketing. A difference in percentages is one way to express the absolute contrast between groups. The comparison also reports a risk ratio and an odds ratio, which express the contrast on relative scales. Absolute and relative measures answer related but not identical questions: the absolute measure describes a difference in event proportions, while relative measures compare the event proportions or odds between groups.

For a binary endpoint, the amount of information depends not only on the observed percentages but also on how many participants contribute outcome data. An estimate based on limited endpoint counts will generally be less precise than the same estimate based on a larger, otherwise similar dataset. The primary confidence interval includes no difference, and the unadjusted p-value is 0.899. That result indicates that the observed data do not provide strong evidence against a no-difference reference under the unadjusted comparison. It does not demonstrate that the treatments are exactly alike, and it does not establish equivalence without an appropriate margin and design.

What do the continuous-outcome summaries show?

Residual stone volume and percentage reduction in stone volume are continuous outcomes summarized by means and standard deviations. For residual stone volume, the reported mean was 14.3 mm³ in the SURE arm and 70.2 mm³ in the basketing arm. For percentage reduction in stone volume, the means were 97.1% and 93.3%, respectively. A mean difference describes the contrast in group averages, while the standard deviation describes how spread out individual measurements are around their group mean.

For residual stone volume, the reported standard deviations were 30.9 mm³ and 144.9 mm³. These values show substantial variation, especially in the basketing arm, relative to its mean. A mean can be affected by a small number of unusually large observations, so a summary based only on means and standard deviations may not fully describe a skewed distribution. Distribution plots, medians, or robust analyses could help characterize such data, but the registry record does not report those details or state that such methods were used. The record also does not report the full individual-level distributions, so the shape and influence of extreme values cannot be determined from these summaries alone.

For percentage reduction in stone volume, the reported standard deviations were 5.4 and 11.7 percentage points as recorded in the outcome summaries. This outcome also has variation across participants, and the spread differs between the arms. The mean difference estimate for this outcome is positive for SURE relative to basketing, while the mean difference estimate for residual volume is negative. The direction of a mean difference must be interpreted in light of the outcome's definition: lower residual volume and higher volume reduction correspond to different numerical directions.

Why do standard errors and confidence intervals matter?

A standard error describes the estimated uncertainty in a statistic arising from sampling variation. It is not the same as the standard deviation: the standard deviation describes variation among participants, whereas the standard error describes uncertainty in an estimated group statistic. The reported standard errors for residual volume are 19.54 for the basketing mean and 4.556 for the SURE mean; for percentage reduction, they are 1.578 and 0.796. The registry's exact calculation methods for these quantities are not stated, so they should be understood as summary precision measures rather than as a complete account of the modeling approach.

A confidence interval gives a range of values compatible with the data and the method used to construct it. Wider intervals indicate less precision; intervals that include no difference leave more uncertainty about the direction and size of a group contrast. The primary endpoint interval includes no difference. The residual-volume interval lies below zero for the SURE-minus-basketing contrast, and the percentage-reduction interval lies above zero. Those intervals describe uncertainty for the unadjusted estimates, but the registry record does not state the confidence level or the full inferential procedure used for every result.

What does over-dispersion mean in general?

In general, over-dispersion means that observed variability is greater than a statistical model expects. It can make standard errors too small if a model assumes less variation than the data contain, leading to confidence intervals that are too narrow and p-values that are too small. This is a general statistical concern, not a reported finding about this study. The registry record does not state that an over-dispersion test or adjustment was performed.

More broadly, the statistical interpretation depends on how outcomes were collected, how missing measurements were treated, which participants were included, and which comparisons were specified in advance. Those details are not reported in the registry entry. The posted comparisons should therefore be viewed as unadjusted summary-based estimates, with the limits that follow from the incomplete account of the original analysis.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate a comparative effect. The primary outcome's point estimates are 48.0% for SURE and 49.0% for standard ureteroscopy with basketing, but a point estimate alone does not show how uncertain the contrast is. The primary comparison's confidence interval includes no difference. That means the interval covers estimates compatible with no group contrast as well as values on either side; the data do not pinpoint a single effect with high precision.

The primary unadjusted p-value is 0.899. A large p-value is not a probability that the treatments are the same, and it does not prove the absence of a meaningful difference. It indicates that, under the tested no-difference reference and the unadjusted calculation, the observed data are not unusual enough to reject that reference. The registry does not report an equivalence margin, so the result cannot be interpreted as a formal equivalence finding.

Precision also varies by endpoint. The residual-volume mean-difference interval runs from -95.22 to -16.58, and does not include zero. The percentage-reduction comparison's interval is on the positive side of zero. The secondary endpoints therefore have estimates whose reported intervals do not include no mean difference, unlike the primary endpoint. However, interval exclusion of zero does not address multiplicity, possible bias from missing measurements, or whether the outcome analyses were planned in advance. Those features affect how much inferential weight to place on the intervals.

Intervals are most useful when read together with the outcome scale, point estimate, and study context. A wide interval may allow both small and substantial effects; a narrower interval can locate the estimate more closely, but does not eliminate systematic error. Here, the registry does not give the confidence level, full analysis specification, or handling of missing observations. The posted intervals can communicate uncertainty around the unadjusted estimates, but they cannot repair these gaps in the record.

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 table and curve are planning illustrations based on the observed effect, not a report of the trial's original design calculations. The figures are participants per arm for 80% power and participants per arm for 90% power. They are not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The illustrated effect to detect is a stated fraction of the observed effect.

The 80% power column gives the number of participants per arm the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect and the analysis model's assumptions held. The 90% power column gives a larger target chance of detection and therefore generally requires more participants per arm for the same effect. These planning values are not the trial's observed enrollment or endpoint sample sizes. They are conditional illustrations, rather than a description of what the completed study was originally designed to detect.

Rows use different fractions of the observed effect. Planning for 75% of the observed effect requires more participants per arm than planning for 100% of the observed effect; planning for 50% requires still more. This is the general relationship expected in power calculations: smaller effects are harder to distinguish from sampling variability and need more information. For the primary endpoint, the listed per-arm values are 24,507 and 32,808 for the 100% row, 43,577 and 58,337 for the 75% row, and 98,065 and 131,281 for the 50% row, with the two entries in each row corresponding to the 80% and 90% power columns.

The record does not report the original sample-size justification or its assumptions. In particular, these illustrations do not establish whether the trial was adequately sized for the primary or secondary outcomes. This is not observed power: observed power calculated from the observed effect largely restates the p-value and does not provide a useful measure of how informative the completed study is. Confidence intervals and the design's prespecified goals are more informative for judging precision.

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 = 0.491; treatment proportion p₁ = 0.478; average p̄ = 0.485.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7068 = 1.3852.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7067 = 0.5948.
4. n = (1.3852 + 0.5948)² / (-0.0126)² = 24,506.7, rounded up to 24,507 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 <- 0.490909090909091                          # control proportion
p1 <- 0.478260869565217                          # 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(4519294)
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 = 24,507 (80% power), 32,808 (90% power)
 75% of observed effect: n per arm = 43,577 (80% power), 58,337 (90% power)
 50% of observed effect: n per arm = 98,065 (80% power), 131,281 (90% power)
power.prop.test: 24506.7 
Simulated power at n = 24,507 per arm: 0.801 (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 two secondary outcomes, but does not report a multiplicity strategy. Multiplicity arises when several hypotheses or outcomes are evaluated: if each is tested separately without adjustment, the chance of at least one apparently unusual result can be higher than for a single planned test. A prespecified hierarchy, family-wise adjustment, or another strategy can address this issue, but the entry does not say whether any such approach was used. The secondary p-values should therefore be read as unadjusted comparisons rather than as results protected against multiple testing.

The record's primary endpoint population is described as patients who met all protocol requirements and had no major deviations that compromised assessment. However, it does not identify how many participants met that definition, how deviations were classified, or whether all randomized participants were included in an intention-to-treat analysis. The posted primary outcome counts are 46 for SURE and 55 for standard basketing, while overall enrollment is 132. The reasons for this difference and the handling of participants without an endpoint result are not reported in the registry record.

Missing data can affect both the estimated outcome rates and their uncertainty, especially if the chance of a missing measurement differs by arm or is related to the outcome. The registry does not report the amount or pattern of missing data, an imputation method, a complete-case rule, or sensitivity analyses. It also does not state whether the same analysis population was used across the primary and secondary endpoints, although the posted group counts are the same for all three.

Other analysis details are also unavailable: the registry does not report a full statistical analysis plan, any covariate adjustment, interim analyses, stopping rules, or the planned confidence level. The analyses entry lists none. The lack of these details does not itself establish that a particular method was or was not used; it means the registry record does not allow those choices to be evaluated. Consequently, the displayed unadjusted comparisons are useful summaries, but they should not be mistaken for a complete account of the trial's prespecified inferential analysis.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: sepsis requiring hospitalization (3.1%).

The registry reports serious adverse events for 1 of 67 participants at risk in the SURE group and 2 of 65 participants at risk in the standard ureteroscopy with basketing group. Other adverse events were reported for 4 of 67 at risk in the SURE group and 5 of 65 at risk in the standard group. No deaths were reported in either group. The serious adverse event term listed among the leading terms was sepsis requiring hospitalization, at 3.1%.

These figures describe the registry's reported adverse-event counts and the group sizes designated as at risk. They do not, by themselves, establish that an event was caused by a procedure or device, or that event rates differ meaningfully between groups. The record does not provide event-specific detail, timing, severity grading beyond the serious-event classification, or a comparative statistical analysis of safety. It also does not explain why the at-risk counts differ from the posted efficacy outcome counts and total enrollment.

Safety comparisons are especially difficult to interpret when event numbers are small: a few observations can change the apparent group pattern substantially, and estimates may be imprecise. The figures should therefore be read descriptively, with the registry's definitions and at-risk denominators, rather than as conclusive evidence of relative safety.

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

The primary endpoint describes the proportion of participants who had no residual fragments on CT at 30 days. The posted rates, 48.0% for SURE and 49.0% for standard ureteroscopy with basketing, are very close, and the unadjusted comparison does not distinguish the groups clearly. This is an account of the observed endpoint summaries and their uncertainty, not proof that the procedures are the same. The registry does not report an equivalence or non-inferiority design or a margin that would permit such a conclusion.

The secondary summaries describe lower mean residual volume and higher mean percentage reduction in the SURE group. These outcomes provide information about volume-based clearance and complement the binary zero-fragment endpoint. Because they are secondary and their p-values are unadjusted, they carry less weight as confirmatory evidence when the multiplicity strategy and analysis plan are unknown. Their observed direction should not be converted into a broad claim about all outcomes or about clinical benefit.

The registry's posted endpoint counts are smaller than overall enrollment, and reasons for that difference are not reported. Missing-data methods and the precise analysis populations are also not reported. If participants were omitted in ways related to outcomes or group assignment, the comparisons could be affected; the record does not permit that possibility to be assessed. Likewise, no individual-level data or sensitivity analyses are reported to show how robust the results are to different assumptions.

The results therefore support a measured interpretation: the primary outcome estimates are close, with uncertainty that includes no difference, while the posted secondary volume summaries have numerical differences and unadjusted p-values below 0.05. Those findings answer different statistical questions and have different inferential limitations. The registry entry does not establish what would happen in other settings, in longer follow-up, or on outcomes not listed in the record. It also does not provide enough methodological detail to reconstruct every step of the original statistical analysis.

Statistical evidence is not the same as a treatment recommendation. These summaries describe what was observed in the registered comparison and how precisely the posted estimates locate group differences. Decisions about care require broader clinical evidence and individual context, which are outside the scope of these registry results.

17. Why This Trial Matters Statistically

This trial illustrates why a primary endpoint should be interpreted according to its exact definition. Zero residual fragments is a threshold outcome: it records whether participants reached a specified imaging state, but not how much stone remained among those who did not reach that state. Residual volume and percentage reduction preserve more gradation, so they may show a different pattern from the binary endpoint without contradicting it.

It also demonstrates the distinction between an estimate and its uncertainty. Similar observed primary percentages do not prove equivalence, and a non-significant p-value does not show that there is no effect. Confidence intervals are needed to understand the range of effects compatible with the data, while a prespecified equivalence margin would be needed to make a formal equivalence claim. The registry does not report such a margin.

The secondary findings emphasize the importance of multiplicity and analysis transparency. Several outcomes can be informative, but unadjusted results across outcomes should not be treated as if each were the sole planned test. Without the original analysis plan, missing-data approach, and population definitions, readers cannot fully judge how confirmatory each secondary result was intended to be.

Finally, the difference between total enrollment and endpoint counts is a practical reminder that randomized enrollment does not necessarily equal the number contributing data to every outcome. Clear reporting of exclusions, missing observations, and analysis populations is essential for judging both representativeness and precision. These considerations are central to interpreting clinical trial evidence, even when outcome summaries and p-values are available.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

A notable limitation in the registry record is the absence of a full account of the statistical analysis plan. It does not state the original sample-size justification, planned treatment-effect assumptions, confidence level, multiplicity strategy, or whether covariate-adjusted analyses were planned. The sample-size illustrations based on observed effects do not fill that gap.

The registry reports enrollment of 132 but gives primary endpoint arm counts of 46 and 55. It does not explain the difference, document participant flow, or describe the analysis population used for each endpoint in sufficient detail to reconcile those figures. The record also does not give missing-data counts, reasons for missingness, imputation methods, or sensitivity analyses. These omissions make it difficult to determine how completely the posted summaries represent the randomized groups.

For the continuous secondary outcomes, the record provides means and standard deviations but not distributional summaries that would show skewness or the influence of extreme observations. This matters particularly for residual volume, where the reported spread is large relative to the SURE mean and is also large in the standard arm. The record does not describe diagnostic checks or alternative analyses that might address non-normal distributions.

Although central reviewers were blinded for the primary CT assessment, the overall masking entry is NONE. The registry does not report additional details about the implementation of image review or any safeguards beyond the stated blinded central review. The entry also does not provide follow-up beyond the 30-day outcome timeframe for the posted efficacy measures, so these results do not characterize later outcomes.

Safety reporting is limited to adverse-event counts, at-risk group sizes, and a listed serious event term. The registry does not supply event narratives, timing, adjudication methods, or comparative safety analyses. These reporting limitations constrain interpretation of both efficacy and safety, and should be kept distinct from the numerical results themselves.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Laser Lithotripsy With and Without Steerable Ureteroscopic Renal Evacuation (SURE) — NCT04519294.
• Registry record last updated 2026-02-27; status last verified 2026-02.
• Results first posted 2026-01-27.
• 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 prospective randomized parallel-group study sponsored by Calyxo, Inc., comparing SURE using the CVAC aspiration system with standard ureteroscopy using basketing after laser lithotripsy. Enrollment was 132, and the study is listed as unmasked overall. The primary endpoint was zero residual fragments on non-contrast CT at 30 days, assessed by blinded central reviewer(s).

Posted primary rates were 48.0% for SURE and 49.0% for standard basketing, with an unadjusted p-value of 0.899. The two secondary outcomes were residual stone volume and percentage reduction in stone volume. Their posted unadjusted comparisons favored SURE numerically, but the registry does not report a multiplicity strategy or sponsor analyses. Endpoint counts are lower than enrollment, and the record does not explain the difference or describe missing-data handling. Interpretation should therefore account for both the outcome-specific results and the substantial limits in reporting of the original analysis.