Efficacy and Safety of Tenalisib (RP6530), in Patients With Locally Advanced or Metastatic Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Tenalisib (RP6530), in Patients With Locally Advanced or Metastatic Breast Cancer (NCT05021900), a randomized phase 2 study. The primary outcome is Percentage of Patients Without Disease Progression.

2. Clinical Question

The clinical question is whether the posted outcomes differ between the two tenalisib dose groups. Both groups received the same drug, so the comparison concerns dose level rather than tenalisib versus no tenalisib. The registry record describes this as a study of preliminary efficacy and safety, and identifies the primary outcome as the percentage of patients without disease progression.

For the primary outcome, the posted counts are 7 of 20 participants in the 800 mg twice-daily group and 8 of 20 in the 1200 mg twice-daily group. These are small groups, so the observed difference is descriptive and its precision matters. The endpoint is framed around disease progression at approximately 6 months; it is not a measure of overall survival or of how long each participant remained progression-free.

The clinical question also has to be read in light of the open-label design, the two-dose comparator, and the limited information about outcome handling. The registry record does not report the original sample-size justification, details of how missing endpoint assessments were treated, or an analysis population definition. These omissions affect how completely the posted comparison can be interpreted.

3. Trial Design

The registry describes a completed Phase II, randomized, open-label, parallel, two-arm study. It lists 40 participants enrolled and reports 20 participants in each dose group. One group received tenalisib 800 mg twice daily as a single agent; the other received tenalisib 1200 mg twice daily as a single agent. There was no masking, and the posted comparison is between the two active dose levels.

The study was sponsored by Rhizen Pharmaceuticals SA. The registry lists a start date of 2021-10-13, a primary completion date of 2023-03-31, and a completed status. Those dates describe the registered study record; they do not by themselves establish how long individual participants were followed or when each outcome was assessed.

The primary outcome is titled “Percentage of Patients Without Disease Progression,” with participants as the measurement unit and an approximate 6-month timeframe. The registry defines progression using RECIST v1.0: a 20% increase in the sum of the longest diameter of target lesions, a measurable increase in a non-target lesion, or the appearance of new lesions. The primary posted results are counts of participants in each group, rather than continuous measurements of tumor size or individual time-to-progression data.

Secondary outcomes listed include overall response rate, clinical benefit rate, progression-free survival, and treatment-emergent adverse events. The posted secondary outcome details include overall response rate and clinical benefit rate at approximately 18 months, as well as safety counts. The registry record does not report a protocol-level account of randomization procedures, allocation concealment, masking of outcome assessment, the original sample-size justification, or the detailed statistical plan. Such details should not be inferred from the brief design labels.

Because the study is open-label and compares two doses, the estimates describe this registered comparison. They do not isolate tenalisib’s effect against an untreated or standard-treatment comparator. The group counts and the registry’s design description are the available basis for interpreting the posted results.

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 Percentage of Patients Without Disease Progression, measured over Approximately 6 months.

The primary endpoint counts participants reported without disease progression at approximately 6 months. The registry’s title describes this as a percentage, while its measurement unit and posted values are participant counts. The progression definition follows RECIST v1.0 and includes specified changes in target lesions, non-target lesions, or new lesions.

This kind of endpoint is used to describe whether participants have met a predefined progression criterion at a clinically specified assessment period. It gives a binary summary for each participant: counted as without progression or not counted in that category. In general, a clearly defined threshold can make the endpoint easier to interpret across participants than an unstructured judgment, although the recorded result still depends on assessment timing, measurement quality, and how missing assessments are handled.

The posted result is 7 participants in the 800 mg twice-daily group and 8 in the 1200 mg twice-daily group, with 20 participants in each group. The registry record does not report the detailed assessment schedule, the handling of participants without an evaluable assessment, or a definition of the analysis population used for this endpoint. It also does not provide individual time-to-event data in the primary result. Therefore, these counts should not be read as a duration of progression-free time or as an estimate of overall survival.

In general, a single assessment at an approximate timeframe and a time-to-event endpoint answer different questions. A participant count at a stated time summarizes status at that assessment; a time-to-event analysis uses the timing of events and may account for censoring. The registry’s primary posted measure is a count, and the record does not post an analysis for it that supplies additional timing information.

7. Results Posted in the Registry

• Tenalisib 1200 mg BID: 40.0% (8/20) versus 35.0% (7/20) on control; risk difference 5.0 percentage points (95% CI -25.0 to 35.0), risk ratio 1.14 (0.51–2.55); unadjusted two-proportion z-test p = 0.744.

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.

Overall Response Rate (ORR)

• 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:
  • Tenalisib 1200 mg BID: 15.0% (3/20) versus 10.0% (2/20) on control; risk difference 5.0 percentage points (95% CI -15.4 to 25.4), risk ratio 1.50 (0.28–8.04); unadjusted two-proportion z-test p = 0.633.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tenalisib 1200 mg BID and the control. The interval gives the range of effects that remain compatible with the data.

Clinical Benefit Rate (CBR)

• 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:
  • Tenalisib 1200 mg BID: 60.0% (12/20) versus 55.0% (11/20) on control; risk difference 5.0 percentage points (95% CI -25.6 to 35.6), risk ratio 1.09 (0.64–1.86); unadjusted two-proportion z-test p = 0.749.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tenalisib 1200 mg BID and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary binary outcomes follow the same broad numerical pattern as the primary result: the 1200 mg group has a somewhat higher count than the 800 mg group for each listed response or benefit measure. This direction is consistent across the posted primary and secondary counts, but the differences are small in the context of the group sizes. The secondary results therefore do not provide a sharply distinct pattern from the primary outcome.

Overall response rate and clinical benefit rate address aspects of tumor response and benefit that are related to, but not identical with, being without progression at the primary assessment. In general, related endpoints can offer complementary views of outcome, but they should not be treated as interchangeable. Their assessment timing and definitions matter, and the registry record does not report detailed definitions for these secondary measures beyond their titles and approximate 18-month timeframes.

The registry lists progression-free survival and treatment-emergent adverse events among secondary outcomes, but the posted secondary outcome details do not include complete results for every listed measure. The registry record does not report an analysis for the posted secondary outcome comparisons. Their recalculated estimates are unadjusted and should be understood as exploratory descriptions rather than confirmatory tests.

Multiple outcomes increase the chance that at least one result appears notable by chance if each is assessed separately. In general, a prespecified hierarchy or multiplicity adjustment can help control that interpretive problem. The registry record does not report such a plan or correction. For that reason, the secondary results carry less evidential weight than a single prespecified primary analysis would, especially given the small groups and the lack of reported sponsor analyses.

Viewed together, the secondary outcomes provide context around the primary count but do not remove its uncertainty. Similar directions across several measures can be noted descriptively; they do not establish a dose-response relationship, demonstrate consistency of treatment effect, or substitute for a defined analysis plan.

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

• Overall Response Rate (ORR)
• Clinical Benefit Rate (CBR)
• Progression Free Survival (PFS).
• Treatment Emergent Adverse Events (TEAEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The outcome is binary at the participant level: participants are counted in the category “without disease progression” or not. In general, binary outcomes can be summarized as counts and proportions in each group. Here, the posted primary counts are 7 of 20 and 8 of 20. The registry gives the corresponding group proportions as 0.35 and 0.4 in the comparison details.

What does the risk difference express?

The risk difference subtracts the proportion in the comparator group from the proportion in the other group. In this comparison, the 1200 mg twice-daily group is compared with the 800 mg twice-daily group, and the posted risk difference is 0.05. A positive estimate means the observed proportion is higher in the first group named in the comparison; it does not, by itself, show that the underlying population difference is positive. The confidence interval describes uncertainty around that estimated contrast.

In general, the risk difference is expressed on an absolute scale and can be easier to relate to group proportions than a ratio measure. The risk ratio instead compares the proportions as a ratio, while the odds ratio compares the odds. These measures answer related but distinct questions and can have different numerical values. The registry’s posted comparison includes ratio estimates as well, but the interpretation emphasizes the risk difference because the primary outcome is a participant count and the direct absolute contrast is straightforward.

What does the p-value tell us?

The posted primary p-value is unadjusted and equals 0.744. In general, a p-value is calculated under a null hypothesis and an analysis model; it indicates how unusual data at least this discrepant would be under that model. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. A p-value should be read together with the estimate, its confidence interval, the study design, and the analysis assumptions.

The registry record does not report the sponsor’s statistical test or a model-based primary analysis. The recalculated comparison is a simple unadjusted calculation from the posted summary statistics. It is not a substitute for a prespecified analysis that might account for design features, missing data, stratification, or other covariates. No adjustment for these features is reported in the registry record.

Why are confidence intervals important?

In general, a confidence interval gives a range of values compatible with the data and the method used, at the stated confidence level. Narrower intervals indicate greater precision; wider intervals indicate greater uncertainty. For the primary risk difference, the posted interval extends across zero, so it is compatible with a difference favoring either dose as well as no difference. The interval is broad relative to the point estimate, reflecting the limited information in groups of 20 participants.

Confidence intervals do not account automatically for all sources of uncertainty. Their interpretation depends on the analysis method and assumptions, and an interval for an unadjusted estimate does not resolve concerns about missing outcomes, measurement, multiplicity, or selection of the analysis population. The registry record does not report enough detail to evaluate those issues fully.

What does over-dispersion mean for this result?

In general, over-dispersion means that observed variability is greater than a statistical model expects. It is a concern for some outcome types and models, such as count models, and can make standard errors too small if ignored. The primary outcome is posted as a binary participant count, not as a repeated-event count or continuous measure. The registry record does not report an over-dispersion assessment or a model that would allow one to evaluate it. No conclusion about over-dispersion should be inferred from these summary counts.

What is and is not reported about the analysis?

The registry identifies the study as randomized and parallel, and the arm sizes are equal in the posted results. It does not report randomization details, a primary analysis population, a missing-data method, covariate adjustment, or the test used for the sponsor’s primary result. The record lists no posted analyses for the outcome comparisons. Consequently, the recalculated contrasts are descriptive, unadjusted summaries rather than a complete account of the trial’s prespecified inferential analysis.

In general, randomized assignment supports a comparison between groups when outcomes are analyzed according to the assigned groups and follow-up is handled appropriately. That interpretation also depends on maintaining the randomized groups, outcome ascertainment, and addressing missing observations. The registry record does not provide enough information to confirm those analysis details. The randomized design is relevant context, but it does not eliminate uncertainty or replace reporting of the analysis methods.

11. Confidence Intervals and Precision

The primary risk-difference estimate for 1200 mg versus 800 mg is 0.05, based on 7 of 20 participants and 8 of 20 participants, respectively. The confidence interval is wide and crosses zero. This means the posted data are compatible with no difference and with differences in either direction; they do not tightly locate the underlying contrast. The unadjusted p-value of 0.744 is consistent with the lack of a precise separation between the groups, but it is not proof that the doses are equivalent.

In general, a confidence interval reflects sampling uncertainty under the method used. A broad interval often arises when a study has limited information, including when group sizes are small or outcomes are uncommon. The interval should not be interpreted as a range containing every plausible value with certainty, nor does it address unmeasured bias, missing outcomes, or the effects of selecting among multiple outcomes.

The primary interval is particularly important because the observed point estimate alone is small in absolute terms. Without the interval, readers might overemphasize the direction of the point estimate. With it, the uncertainty is more apparent: the posted data do not support a precise estimate of the dose contrast.

The secondary outcome comparisons are also based on 20 participants per group and have their own uncertainty. Their intervals are broad, and the registry does not report formal analyses for those outcomes. The safety counts are likewise descriptive and do not include comparative confidence intervals in the posted record. Overall, the available precision is limited, and conclusions should remain proportionate to that uncertainty.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these binary outcomes, the listed figures are participants per arm, not total participants. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were present. The 90% power column applies the same idea with a 90% chance. In general, higher target power requires more participants when other assumptions are held fixed. Smaller effects are harder to distinguish from random variation, so the planning illustrations require more participants per arm when the effect to detect is reduced from the observed effect.

For these calculations, the effect is based on the difference observed in this small study. It may not represent the effect that would be expected in a future study. The figures therefore illustrate how sample size changes with the selected effect and power targets; they are not a proposed enrollment target and do not establish what the original investigators planned. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

These figures are not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after a study is complete. The trial results are best read directly through the posted group counts, estimated contrast, and uncertainty, while the sample-size figures serve as hypothetical planning illustrations.

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 = 0.350; treatment proportion p₁ = 0.400; average p̄ = 0.375.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6847 = 1.3419.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6837 = 0.5754.
4. n = (1.3419 + 0.5754)² / (0.0500)² = 1,470.5, rounded up to 1,471 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 <- 0.35                          # control proportion
p1 <- 0.4                          # 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(5021900)
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 = 1,471 (80% power), 1,969 (90% power)
 75% of observed effect: n per arm = 2,598 (80% power), 3,477 (90% power)
 50% of observed effect: n per arm = 5,804 (80% power), 7,769 (90% power)
power.prop.test: 1470.5 
Simulated power at n = 1,471 per arm: 0.798 (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 record identifies a primary endpoint and lists several secondary outcomes, but it does not report a hierarchy for testing them, a family of hypotheses, or a multiplicity adjustment. In general, testing multiple outcomes can increase the chance of at least one apparently unusual result under a setting where none of the underlying effects differs. A prespecified approach helps readers distinguish a primary confirmatory question from secondary or exploratory analyses. Without that information, the secondary comparisons should be interpreted cautiously and their unadjusted p-values should not be treated as confirmatory evidence.

The posted secondary comparisons have unadjusted p-values, but no reported analyses are listed for those endpoints. The registry record also does not report whether interim analyses were planned or conducted, whether any stopping rules were used, or whether the posted analysis followed a prespecified statistical plan. Those details are not reported in the registry record and should not be inferred.

Missing-data handling is also not described in the available record. It does not state how participants without an evaluable progression assessment were classified, whether missing outcomes were imputed, or whether the analysis used all randomized participants or another population. In general, missing outcomes can affect both the estimated group proportions and their uncertainty, particularly when the reasons for missingness differ between groups. The posted counts alone do not resolve how these issues were addressed.

The registry does not report a detailed analysis population definition, such as whether the primary comparison followed randomized assignment or used participants with evaluable data. It also does not report a sensitivity analysis for missing outcomes. These omissions limit assessment of whether the reported counts represent the full randomized groups and how robust the result is to alternative assumptions.

These gaps are reporting limitations, not evidence that a particular method was or was not used. They mean that the posted record supports a descriptive account of the counts and unadjusted contrasts, but not a full evaluation of multiplicity control, missing-data assumptions, interim monitoring, or analysis-population choices.

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: pulmonary embolism (10.0%), hypersensitivity (5.0%), covid-19 (5.0%), death (5.0%).

The safety figures are counts within each group. The registry reports serious adverse events in 5 of 20 participants in the 800 mg twice-daily group and 1 of 20 in the 1200 mg twice-daily group. Other adverse events are reported in 15 of 20 and 17 of 20 participants, respectively. Deaths are listed for 2 participants in the 800 mg group and 1 participant in the 1200 mg group.

These figures should be read descriptively. The registry record does not provide event-level timing, duration, attribution to treatment, exposure-adjusted rates, or details about how events were collected. It does not establish that the listed deaths were caused by treatment. Serious adverse events, other adverse events, and deaths are distinct categories in the posted safety information and should not be assumed to be mutually exclusive.

The registry also lists pulmonary embolism at 10.0%, hypersensitivity at 5.0%, COVID-19 at 5.0%, and death at 5.0% among the top serious terms. These term percentages do not on their own establish comparative risk between dose groups or causality. Given the small groups and the absence of a detailed safety analysis in the registry record, the counts are signals for description rather than precise estimates of the relative safety of the doses.

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

The posted primary result describes the number of participants reported without disease progression at approximately 6 months in each tenalisib dose group. The counts differ by one participant, and the unadjusted risk difference is 0.05. The confidence interval is broad and crosses zero, so the data do not precisely establish the direction or size of a difference between the two doses.

This finding does not show that the doses are equivalent. Equivalence requires a prespecified clinically acceptable range and an analysis designed to assess whether the full confidence interval lies within that range. The registry record does not report such a design. Nor does the p-value establish that there is no difference; it indicates that the unadjusted comparison does not sharply distinguish the observed data from a no-difference model under the analysis used.

The study compares two active doses and does not include a placebo or a different-treatment group. Therefore, the posted comparison cannot by itself establish what would have happened without tenalisib or relative to another treatment. It also cannot establish an effect beyond the studied population and setting. The record describes the study as assessing preliminary efficacy and safety, and the small groups and incomplete analysis details reinforce that the results are descriptive and uncertain.

The secondary outcome counts add context but are not formal confirmation of the primary result. No multiplicity approach or sponsor analyses are reported for those comparisons. Likewise, the safety counts describe events observed in the two groups but do not establish causal attribution or a precise comparative safety profile.

In general, trial results are most informative when read with their design, outcome definitions, estimates, confidence intervals, missing-data methods, and analysis plan. Several of those details are not reported in the registry record. The most defensible interpretation is therefore limited: this completed Phase II study recorded similar primary counts across two tenalisib dose groups, with substantial uncertainty around the unadjusted contrast and incomplete reporting for several analytic details.

17. Why This Trial Matters Statistically

This trial is statistically informative as an example of how a randomized design and a small sample can coexist with substantial uncertainty. Randomization creates a framework for comparing assigned groups, but it does not make estimates precise when each group contains 20 participants. The primary point estimate is easy to state; the confidence interval is essential for understanding how much the observed data leave unresolved.

The comparison also illustrates the value of stating the contrast in absolute terms. A risk difference of 0.05 communicates the observed difference on the scale of group proportions. It remains important to consider the interval around that value, because a point estimate from small groups can move substantially with a small change in participant counts.

The record distinguishes a preliminary two-dose comparison from a trial with a control group receiving no tenalisib or another treatment. That design determines which causal question can be addressed. It also highlights that conclusions about a relative dose contrast are not interchangeable with conclusions about treatment benefit versus an external comparator.

The secondary outcomes and safety counts show why transparent reporting matters. A record that identifies outcomes but does not include complete analyses, an analysis population, missing-data methods, or multiplicity handling leaves readers unable to fully evaluate the inferential framework. These are not minor details: they determine how much weight to give multiple comparisons and how to understand who contributed to each result.

Finally, the sample-size illustrations demonstrate how planning requirements depend on the effect selected for detection and the desired power. Because the illustration uses the observed effect and not the original design justification, it should not be mistaken for evidence about the trial’s intended statistical power. The distinction between planning scenarios and completed-study precision is central to responsible interpretation.

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.

The registry record offers limited detail beyond the trial design labels and posted outcome summaries. It does not report baseline characteristics, full eligibility criteria, randomization methods, allocation concealment, or the schedule and procedures used for outcome assessment. These omissions make it difficult to assess group comparability at baseline, the potential for assessment bias in an open-label study, or the applicability of the results to particular patient subgroups.

The primary endpoint is described at approximately 6 months, but the record does not provide participant-level assessment timing or explain how participants without an evaluable assessment were handled. The posted count therefore cannot be interpreted as a complete time-to-event analysis. The registry record also does not report an analysis population definition, missing-data method, or sensitivity analysis.

The study has 20 participants per arm and compares two active dose levels. This limits precision and does not provide a no-tenalisib or other-treatment comparator. The randomized design is relevant to the dose comparison, but it does not answer comparisons outside the two groups studied. The registry describes preliminary evaluation, and the posted results should be interpreted within that scope.

Secondary outcome reporting is incomplete relative to the outcomes listed in the record. The registry reports no analyses for the posted secondary comparisons and does not describe multiplicity control, an outcome hierarchy, or interim analyses. Detailed definitions for the response and clinical-benefit measures are not reported in the record information.

Safety reporting is also limited to group counts and selected serious-event terms. Attribution, timing, duration, exposure, and event-level details are not reported. Small groups and limited safety-analysis detail make the counts unsuitable as precise comparative estimates. These limitations concern the information documented in the registry record; they do not establish what methods may have been used outside that record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Tenalisib (RP6530), in Patients With Locally Advanced or Metastatic Breast Cancer — NCT05021900.
• Registry record last updated 2024-08-13; status last verified 2024-08.
• Results first posted 2024-08-13.
• 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

NCT05021900 is a completed, randomized, open-label Phase II parallel-group study of tenalisib in patients with locally advanced or metastatic breast cancer. The registry lists 40 participants: 20 assigned to tenalisib 800 mg twice daily and 20 to tenalisib 1200 mg twice daily.

The primary outcome was the number of participants without disease progression at approximately 6 months, defined using RECIST v1.0. The posted counts are 7 and 8, respectively; the unadjusted risk difference is 0.05, with a broad confidence interval spanning zero and an unadjusted p-value of 0.744. Secondary response and clinical-benefit counts and group safety counts are also posted.

The record does not report the original sample-size justification, a detailed statistical analysis plan, analysis populations, missing-data handling, or multiplicity procedures. The results are therefore best read as descriptive evidence from a small two-dose comparison, with limited precision and incomplete analytic detail.