Rasburicase in Patients at High Risk for Tumor Lysis Syndrome (TLS) During Cycle-2: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rasburicase in Patients at High Risk for Tumor Lysis Syndrome (TLS) During Cycle-2 (NCT01200485), a randomized phase 2 study. The primary outcome is Number of Participants (Incidence) of LTLS (Laboratory Tumor Lysis Syndrome).

2. Clinical Question

The study asks whether using rasburicase for two cycles can control or prevent tumor lysis syndrome better than using rasburicase for one cycle followed by allopurinol for one cycle. The posted primary result addresses the comparison in randomized cycle 2, after rasburicase in cycle 1. It counts participants meeting the laboratory definition of tumor lysis syndrome; it is not a measure of symptoms, survival, or overall disease response.

The clinical question is comparative, but the event counts are sparse: one participant in the rasburicase arm and one in the allopurinol arm met the primary endpoint. The estimated risk difference and its confidence interval express the comparison in a way that includes both the direction and the uncertainty of the estimate. The registry record does not report a conclusion about which treatment strategy was preferable, and the event counts alone do not establish equivalence or a difference.

The study also assessed safety. Its stated goal included studying safety, but the primary efficacy result should be read separately from the adverse-event counts. Those counts describe reported events in the listed groups and do not, by themselves, establish that a particular event was caused by treatment.

3. Trial Design

The registry record identifies this as a phase 2 randomized study with no masking. It lists an enrollment of 55 and a completed status. The study title and summary concern rasburicase over two chemotherapy cycles compared with rasburicase in cycle 1 followed by allopurinol in cycle 2. The primary endpoint, however, is specifically assessed during cycle 2.

In cycle 1, the arm description states that participants received rasburicase by vein on day 1, at 0.15 mg/kg or a flat dose of 3 mg, with additional dosing as needed until day 5. The cycle lasted 21 days. For cycle 2, participants were randomized to rasburicase or allopurinol. The rasburicase description specifies 0.15 mg/kg by vein on day 1, with additional dosing as needed until day 5. The allopurinol description specifies 300 mg/day by vein on days 1–5.

The primary analysis population is described as all 46 participants treated in randomized cycle 2. The posted arm sizes are 21 for rasburicase and 25 for allopurinol. The record does not explain why the analysis population is smaller than the total enrollment, or give details about participants who were not included in the randomized-cycle-2 analysis.

There is a design-label tension in the record: it identifies random allocation and gives two cycle-2 arms, while also listing a single-group model. The record does not explain this classification. It also does not report the original sample-size justification, the intended statistical analysis plan, or other design details such as stratification or an allocation ratio. Those details should not be inferred from the posted results or from the planning illustration.

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: Cycle 2 is the study cycle; of the 55 participants enrolled on study, 52 were treated in cycle 1 (rasburicase alone), and only 46 were randomized onto the two arms in the study cycle (cycle 2, Arm A: Rasburicase; Arm B: Allopurinol).

Cycle 1: Rasburicase Alone Delivery

Reasons for not completing this period:

Cycle 2: Randomization

Analysis population for the primary outcome, as defined in the registry: All 46 participants treated in randomized cycle 2 of study were included in analysis.

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.

Population: Of 55 enrolled on study, 52 participants were treated in Cycle 1 Rasburicase alone, only 46 randomized to Cycle 2 Arm A Rasburicase (21) and Arm B Allopurinol (25).

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants (Incidence) of LTLS (Laboratory Tumor Lysis Syndrome), measured over Up to two 3-week cycles, 6 weeks.

The primary endpoint is the number of participants who developed laboratory tumor lysis syndrome (LTLS) during cycle 2. The timeframe is up to two 3-week cycles, or 6 weeks, while the endpoint definition specifies that LTLS is assessed during cycle 2. The reported unit is participants, so the outcome is a count of people meeting the definition, rather than a continuous laboratory measurement or a time-to-event measure.

The registry record defines LTLS using the Cairo-Bishop criteria. The criteria consider uric acid, potassium, phosphate, and calcium. A qualifying change can be a value at or beyond a stated threshold or a change of at least 25% from baseline. The definition requires qualifying changes in at least two of the listed serum values within the stated window around chemotherapy initiation: within 3 days before or 7 days after initiation.

This endpoint is used to identify a laboratory pattern associated with tumor lysis syndrome, rather than to count any single abnormal laboratory result as a case. In general, a prespecified composite laboratory definition can provide a consistent rule for classifying participants across treatment groups. Its interpretation depends on applying the same criteria and assessment window to both groups. The registry record gives the criteria and timeframe but does not report further details about laboratory collection schedules, adjudication, or how incomplete laboratory data were handled.

The primary result is one participant with LTLS in each arm. That count is the direct observed outcome; the comparative estimate and confidence interval add a measure of how uncertain the between-arm contrast is.

7. Results Posted in the Registry

• Arm B (Allopurinol): 4.0% (1/25) versus 4.8% (1/21) on control; risk difference -0.8 percentage points (95% CI -12.7 to 11.2), risk ratio 0.84 (0.06–12.63); unadjusted two-proportion z-test p = 0.900.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the event count represent?

The primary endpoint is binary at the participant level: each participant either met the registry definition of LTLS during cycle 2 or did not. The arm summaries report the number of participants with the event, alongside the number included in each group. In this study, the posted counts are one event among 21 participants assigned to rasburicase and one among 25 assigned to allopurinol. Because the outcome is a count of participants with an event, it should not be interpreted as a count of abnormal laboratory readings or episodes.

In general, a binary endpoint is often summarized by an event risk within each group and by a contrast between those risks. A risk difference expresses an absolute difference on the risk scale. The registry record posts a risk difference of -0.008 for the listed comparison. The precise direction convention for the comparison is not described in prose in the record; the estimate should therefore be read with the arm labels and displayed comparison together rather than assigning an unverified subtraction order.

What does the p-value tell the reader?

The posted unadjusted p-value is 0.9. In general, a p-value describes the degree of compatibility between the observed data and a specified null model, assuming the analysis model and test are appropriate. It is not the probability that a treatment effect is absent, and it does not quantify the size or clinical importance of a difference. The record does not give additional details about the test used to produce this p-value. Because it is identified as unadjusted, it should not be presented as a multiplicity-adjusted result.

For a sparse binary outcome, a small number of events can make estimates sensitive to the observed counts and the method used. General methods for binary outcomes may use different approximations or exact procedures, and their behavior can vary when events are rare. The registry record does not specify enough about the test or estimation procedure to identify which methodological choices were made. No alternative method should be attributed to the study without that information.

How should the confidence interval be read?

In general, a confidence interval gives a range of values compatible with the data under the interval method and its assumptions. It is not a guarantee that the true effect lies in the reported range, nor is it a range of individual participant outcomes. For the posted risk difference, the 95% confidence interval runs from -0.127 to 0.112. Since it includes zero and values on both sides, the data do not pin down the direction of the risk difference. Its width also signals substantial uncertainty in the comparison.

Confidence intervals are especially useful alongside a p-value because they show the scale and range of uncertainty rather than reducing the result to a threshold decision. In this trial, the small number of events means that the interval is more informative about imprecision than a simple statement that the comparison was or was not statistically significant. The registry record does not identify the confidence-interval method, so no specific method should be assumed.

Why can sparse events make estimates imprecise?

In general, the precision of a group comparison depends partly on how much information the data contain. Event counts contribute information about the event risk, and very few events leave many plausible underlying risks consistent with the observations. When events are rare, a small change in the observed count can have a substantial effect on an estimated risk or relative measure. The observed counts are one event in each arm, which limits the information available for a precise contrast.

Over-dispersion is a general concern when observed variability is greater than a chosen model expects. It can lead to standard errors or confidence intervals that are too small if the extra variability is ignored. The primary endpoint is binary, and the record does not report an over-dispersion assessment or a model that assumes a dispersion parameter. This general concept should not be taken to mean over-dispersion was present or analyzed in this study.

What can the planning illustration show?

The sample-size illustration is based on the observed effect, not on the trial's original design. Its stated assumptions are a two-sided significance level of 0.05, equal allocation between arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original sample-size justification and the assumptions used to design the trial are not reported in the registry record.

Under the row described as planning for 100% of the observed effect, the illustration gives 11,327 participants per arm for 80% power and 15,163 participants per arm for 90% power. Planning for 75% of the observed effect gives 20,555 participants per arm for 80% power and 27,517 participants per arm for 90% power. Planning for 50% of the observed effect gives 47,187 participants per arm for 80% power and 63,169 participants per arm for 90% power. These are planning illustrations, not observed trial requirements or evidence about what the original investigators intended.

In general, power is the probability that a study will detect a specified effect under stated assumptions if that effect is real. Higher target power generally requires a larger sample, and smaller effects generally require more participants to detect. The figures depend on the stated planning assumptions and the observed-effect basis; they should not be generalized as a design recommendation for other studies.

10. Confidence Intervals and Precision

The posted risk-difference estimate is -0.008, with a 95% confidence interval from -0.127 to 0.112. The interval covers zero as well as values on either side of zero. Thus, the data do not tightly determine the direction or size of the between-arm difference. The interval is the key precision measure for this comparison: it conveys considerably more than the point estimate alone, which is only one value selected by the estimation procedure.

In general, a confidence interval is a range generated by a statistical method that, under its assumptions, reflects uncertainty about an underlying parameter. It does not mean that every value in the range is equally likely, and it does not describe the range of outcomes among individual participants. A wider interval indicates less precision than a narrower interval for the same type of estimate. The registry record does not state the method used to construct this interval, so its method-specific properties cannot be assessed from the record.

The event counts are sparse: one participant in each group met the endpoint. With so few observed events, the comparison has limited information for distinguishing among plausible event risks. The interval includes the null value but also allows nonzero differences in either direction. Accordingly, the result should not be summarized as demonstrating equal risks, and it should not be described as establishing a particular advantage. The p-value of 0.9 is consistent with the uncertainty conveyed by the interval, but it does not replace that interval or quantify the treatment difference.

The reported arm sizes and the analysis population describe the available primary comparison, but the record does not report a missing-data method or an account of participants excluded before cycle 2. These omissions also limit assessment of how broadly the observed precision represents the randomized population. The interval describes uncertainty under the analysis used; it does not account automatically for possible selection or missing-outcome concerns.

11. Planning a Similar Trial: Sample Size

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

The sample-size display is a planning illustration based on the observed effect, not the original trial design. These figures are participants per arm, rather than total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The registry record does not report the original design's sample-size assumptions or justification.

The 80% power column gives the number of participants per arm associated with an 80% probability of detecting the specified effect under those assumptions, if that effect is real. The 90% power column gives the corresponding number per arm for a 90% probability. These are prospective planning quantities, not probabilities that the result of this completed study is correct.

For planning at 100% of the observed effect, the illustration lists 11,327 participants per arm for 80% power and 15,163 participants per arm for 90% power. Planning at 75% of the observed effect gives 20,555 participants per arm for 80% power and 27,517 participants per arm for 90% power. Planning at 50% of the observed effect gives 47,187 participants per arm for 80% power and 63,169 participants per arm for 90% power. The smaller-effect rows require larger sample sizes under the stated assumptions because smaller differences are harder to distinguish from sampling variation.

The planning figures are not observed power. Observed power is not an appropriate substitute for interpreting the result's confidence interval and event counts. The illustration is also not a claim that the study should have recruited these numbers: it uses the observed effect as its starting point, and estimates based on sparse events can be highly uncertain. The original rationale for the study's enrollment is not reported in the registry record.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.048; treatment proportion p₁ = 0.040; average p̄ = 0.044.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2894 = 0.5673.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2894 = 0.2436.
4. n = (0.5673 + 0.2436)² / (-0.0076)² = 11,326.7, rounded up to 11,327 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 <- 0.0476190476190476                          # control proportion
p1 <- 0.04                          # 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(1200485)
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 = 11,327 (80% power), 15,163 (90% power)
 75% of observed effect: n per arm = 20,555 (80% power), 27,517 (90% power)
 50% of observed effect: n per arm = 47,187 (80% power), 63,169 (90% power)
power.prop.test: 11326.7 
Simulated power at n = 11,327 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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record lists two outcome measures, but no secondary result is posted. The primary endpoint result is therefore the only outcome result available for interpretation in this record. It does not state whether other outcomes were assessed, which were prespecified as primary or secondary in the original protocol, or whether any analyses were conducted but not posted.

Multiplicity arises in general when several outcomes, comparisons, time points, or statistical tests are considered. The more analyses that are performed, the greater the opportunity for at least one result to appear unusual by chance if each is interpreted without adjustment. The posted p-value is identified as unadjusted. The registry record does not report a multiplicity plan or whether adjustment was intended, so no adjustment should be inferred.

The record does not report an interim-analysis plan, stopping rules, or monitoring procedures. It also does not report the original statistical analysis plan or the primary sample-size justification. These details matter when evaluating which analyses were planned in advance and how the final result was selected or interpreted. Their absence from the registry record does not establish that such plans did not exist; it means they are not reported in the registry record.

The primary analysis population is stated as all 46 participants treated in randomized cycle 2. The reason that this population differs from the overall enrollment of 55 is not reported. The record does not explain how many participants were randomized before cycle 2, whether any participants did not start cycle 2, or why any participant was not included in the primary analysis. It also does not describe an intention-to-treat analysis or another named analysis population.

Missing-outcome handling is not reported in the registry record. There is no description of whether all participants had the laboratory measurements needed to classify LTLS, how unavailable measurements were handled, or whether sensitivity analyses addressed missing data. These gaps limit assessment of possible bias from exclusions or incomplete endpoint measurement. The design is identified as randomized, but the record's additional single-group model classification is unexplained, making detailed reconstruction of the analysis structure difficult.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: death (4.8%), acute renal failure (3.8%), methemoglobinemia (1.9%).

The registry record reports serious adverse events for 3 of 52 participants in cycle 1, 1 of 21 in cycle-2 Arm A (rasburicase), and 1 of 25 in cycle-2 Arm B (allopurinol). Other adverse events are reported for 38 of 52 participants in cycle 1, 12 of 21 in cycle-2 Arm A, and 17 of 25 in cycle-2 Arm B. The record lists deaths of 0 in cycle 1 and 1 in each cycle-2 arm.

These are counts within the listed safety groups. The cycle-1 group is labelled rasburicase alone, while the two cycle-2 groups correspond to the randomized arms. They should not be treated as if they were three mutually exclusive randomized groups or as a direct randomized comparison across cycles. The registry record does not report a causal attribution for each event or give further detail about event severity beyond the serious-event classification.

The listed top serious-event terms are Death at 4.8%, Acute renal failure at 3.8%, and Methemoglobinemia at 1.9%. The record does not specify the denominator or group assignment for these percentages in the displayed information. These terms and percentages should therefore be read as reported, without assigning them to a particular arm or inferring an individual participant's risk.

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

The observed primary outcome was one participant with laboratory tumor lysis syndrome in each randomized cycle-2 arm. The estimated risk difference was -0.008, and its 95% confidence interval extended from -0.127 to 0.112. The unadjusted p-value was 0.9. Taken together, these statistics describe a comparison with very few observed events and substantial uncertainty about the size and direction of any underlying difference.

The result does not demonstrate that the two cycle-2 strategies have identical effects. A confidence interval containing zero is not proof of equivalence, and the registry record does not describe an equivalence or non-inferiority design or margin. Nor does the p-value establish that there is no difference. The data are too imprecise to support a strong conclusion about the direction or magnitude of the contrast from the primary endpoint alone.

The result also does not establish that one strategy is superior. The observed count is the same in each group, but equal observed counts in a small analysis population do not guarantee equal underlying risks. The interval spans values on either side of zero, which is why the point estimate should not be read as a definitive treatment effect.

The scope is limited to the primary laboratory endpoint in participants included in randomized cycle 2, under the posted Cairo-Bishop definition and assessment window. The result is not a direct estimate of clinical outcomes, long-term effects, or effects in populations not represented in the study. The registry record does not report a secondary result, missing-data methods, or detailed analysis procedures that could broaden or refine the interpretation.

In general, randomized comparisons can support causal inference when the design and analysis are properly implemented, but interpretation also depends on complete outcome ascertainment, adherence to the planned analysis, and sufficient information. The record supplies limited detail on these topics. The appropriate conclusion is therefore descriptive: the posted data record one LTLS event in each arm and an imprecise between-arm estimate, without establishing equivalence or a treatment advantage.

16. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can remain statistically uncertain when the endpoint is rare and the analysis population is small. Although randomization creates a framework for comparing the two cycle-2 strategies, only one primary event was recorded in each arm. The central statistical issue is therefore not simply which arm had the lower observed count; the counts are the same. It is how little information those counts provide about the underlying event risks and their difference.

The confidence interval makes that limitation visible. Its range includes zero and extends to values on both sides, so the point estimate does not resolve the direction of the comparison. The unadjusted p-value is also not a measure of equivalence. Reading the event counts, estimated difference, and interval together avoids turning a sparse result into a stronger claim than it supports.

The registry record also demonstrates why design and analysis details matter. It identifies a randomized phase 2 study and provides two cycle-2 arms, yet lists a single-group model. The primary analysis includes 46 participants, whereas overall enrollment is 55, and the reason for that difference is not reported. These details affect how confidently readers can reconstruct the study population and the intended comparison.

Finally, a planning illustration based on the observed effect is not a substitute for an original sample-size rationale. Its figures depend on explicitly stated assumptions and are sensitive to the uncertain observed effect. Separating such planning quantities from the trial's observed evidence helps prevent a retrospective calculation from being mistaken for the study's original design or for observed power.

17. Limitations

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

The primary analysis includes 46 participants treated in randomized cycle 2, compared with an overall enrollment of 55. The registry record does not explain the difference, identify participants who did not enter cycle 2, or give reasons for exclusion from the primary analysis. This limits assessment of how the analyzed participants relate to all enrolled participants.

Only one participant in each arm met the primary endpoint. This sparse event count makes the risk-difference estimate imprecise, as reflected by its confidence interval from -0.127 to 0.112. The record does not report the method used to calculate the confidence interval or the test underlying the unadjusted p-value, limiting independent assessment of the analysis choices.

The record does not report missing-data procedures, laboratory assessment completeness, or sensitivity analyses. Because LTLS classification depends on multiple laboratory values measured within a defined timeframe, incomplete measurements could affect endpoint classification; whether this occurred is not reported. Adherence, protocol deviations, and treatment exposure beyond the arm descriptions are also not detailed.

The registry labels the design randomized and gives two arms, but also lists a single-group model. No explanation is reported. The original statistical analysis plan, sample-size justification, multiplicity approach, interim analyses, and stopping rules are not reported in the registry record. The record lists two outcome measures but posts no secondary result. These gaps constrain assessment of prespecification and the full analysis context.

The posted primary outcome concerns laboratory tumor lysis syndrome during cycle 2. It does not provide a result for clinical manifestations or longer-term outcomes. The safety counts are reported for different cycle groups, and the record does not give causal attribution for individual events. The serious-event percentages are listed without a denominator or group assignment in the displayed information, so they should not be interpreted as arm-specific rates.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Rasburicase in Patients at High Risk for Tumor Lysis Syndrome (TLS) During Cycle-2 — NCT01200485.
• Registry record last updated 2020-01-31; status last verified 2020-01.
• Results first posted 2020-01-31.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT01200485 is a completed randomized phase 2 study of rasburicase use during two chemotherapy cycles compared with rasburicase during cycle 1 followed by allopurinol during cycle 2. The record lists leukemia and lymphoma as conditions, no masking, and total enrollment of 55.

The primary endpoint is the number of participants with laboratory tumor lysis syndrome during cycle 2 under the Cairo-Bishop criteria. The primary analysis included 46 participants treated in randomized cycle 2: 21 in the rasburicase arm and 25 in the allopurinol arm. One event was recorded in each arm. The estimated risk difference was -0.008, with a 95% confidence interval from -0.127 to 0.112 and an unadjusted p-value of 0.9.

The record posts safety counts for cycle 1 and both cycle-2 arms but no secondary result. It does not report the original sample-size justification, missing-data methods, multiplicity plan, or detailed statistical analysis plan. The primary comparison is therefore best read as a sparse and imprecise result, rather than evidence of equivalence or a definitive difference.