Evidence checked October 31, 2026. Regulatory examples retain their announcement dates. All numerical examples are hypothetical and are not instructions for interpreting an individual's medical test.
1. The intended use is part of the result
When the FDA announced clearance of a blood test to aid Alzheimer's diagnosis on May 16, 2025, it specified a population and a setting. The announcement concerned symptomatic adults aged fifty-five and older and described use in specialized care alongside other clinical information. It explicitly said the test was not a screening or stand-alone diagnostic test. The FDA announcement illustrates a general principle rather than the subject of this article: the words around an accuracy claim define what the evidence supports.
A test does not possess one universal percentage called accuracy that follows it unchanged into every clinic, home, or screening program. Its performance is measured among particular people, with particular samples, operators, thresholds, and reference procedures. Changing those conditions can change the interpretation of the result, even if the device or laboratory method remains the same.
That makes intended use a scientific statement. Is the test meant to help explain symptoms, screen people without symptoms, select patients for another procedure, or monitor a known condition? Each role creates a different population and a different consequence for error. A test useful in one role may be insufficiently evaluated in another.
The central question is therefore not simply whether a new test is good. It is whether the evidence fits the decision being proposed. A careful answer begins before the first performance statistic, with the people and circumstances the statistic is supposed to represent. Without that frame, even a correctly calculated number can invite a misleading conclusion.
2. Four cells explain the basic arithmetic
For a binary test evaluated against an appropriate reference, results can be arranged into four groups: people with the target condition who test positive, people with it who test negative, people without it who test positive, and people without it who test negative. These groups support different measures. Confusing their denominators is one of the easiest ways to misunderstand a diagnostic claim.
Sensitivity asks what fraction of those with the condition test positive. Specificity asks what fraction of those without it test negative. Positive predictive value asks what fraction of positive results belong to people with the condition. Negative predictive value asks what fraction of negative results belong to people without it. The words sound similar because the same four counts are involved, but the questions are different.
A hypothetical test could detect ninety of one hundred affected people and correctly return negative results for nine hundred of one thousand unaffected people. Sensitivity and specificity would both be ninety percent. Yet there would be one hundred ninety positive results: ninety true positives and one hundred false positives. Fewer than half of the positive results would correspond to the target condition in that constructed population.
The arithmetic does not contradict the sensitivity or specificity. It answers a different question. A headline that reports ninety percent accuracy without specifying the measure leaves the reader to supply a meaning, often the wrong one. The most useful report gives the counts or a clearly defined table, so that the relationship between the statistic and the underlying population remains visible.
3. Prevalence changes the meaning of a positive result
Suppose a hypothetical test has ninety percent sensitivity and ninety-five percent specificity. For illustration, hold those properties fixed while changing how common the target condition is in the tested population. This assumption isolates the arithmetic effect of prevalence; real-world sensitivity and specificity may also change when the population changes.
In ten thousand people with a one percent prevalence, one hundred have the condition. The test produces ninety true positives and ten false negatives. Among the nine thousand nine hundred without the condition, five percent, or four hundred ninety-five, test positive. There are five hundred eighty-five positive results, of which ninety are true positives. The positive predictive value is about fifteen percent.
Now consider ten thousand people with a twenty percent prevalence. Two thousand have the condition, producing eighteen hundred true positives. Of the eight thousand without it, four hundred test positive. There are twenty-two hundred positive results, and about eighty-two percent are true positives. The same assumed sensitivity and specificity yield a very different meaning for a positive result.
This is why performance in a specialized referral population cannot simply be pasted onto a broad screening claim. The mix of people being tested matters. A low predictive value in a low-prevalence setting does not necessarily mean the assay has become technically defective; it may follow from the number of unaffected people exposed to the false-positive rate. The appropriate response is to evaluate the intended pathway, including confirmation and consequences, rather than interpreting one percentage in isolation.
4. The patient spectrum can change the test itself
Prevalence is not the only difference between populations. People with early or mild disease may be harder to distinguish from people without the target condition than people with advanced, obvious disease. Other illnesses may produce similar signals. The range of clinical presentations and competing conditions is often called the patient spectrum.
A 2004 methodological paper by Goehring and colleagues examined variation in diagnostic performance across subgroups and distinguished spectrum effects from their consequences for decisions. Its author abstract is a useful reminder that sensitivity and specificity are not immutable physical constants. They are estimates from particular clinical circumstances.
Consider a hypothetical development study comparing patients with severe, unmistakable disease against unusually healthy volunteers. The test may separate those groups exceptionally well. In practice, the relevant challenge may be to distinguish early disease from other causes of similar symptoms. The development study has not necessarily evaluated that harder comparison.
This is different from the pure prevalence calculation in the previous section. There, sensitivity and specificity were deliberately held fixed to show a mathematical effect. Here, the composition of the groups can change the conditional performance itself. Both issues can occur together when a test moves from specialist care to a broader population.
A credible validation therefore describes disease stage, symptom patterns, alternative diagnoses, and the route by which participants entered the study. It does not assume that a large sample compensates for a poorly matched spectrum. Thousands of easy examples can provide precise evidence about an easy distinction while leaving the intended clinical distinction uncertain.
5. Recruitment determines which mistakes are visible
A diagnostic study can recruit people because they are undergoing evaluation for the relevant problem, or it can assemble separate collections of known cases and controls. Each design can serve a purpose, but they do not necessarily provide the same evidence about real-world use. The selection process determines which borderline and confusing situations appear in the data.
A hypothetical case-control study might be an efficient early test of whether a biomarker contains any useful signal. That is a legitimate development question. If the same study is used to claim performance in an ordinary clinic, however, readers need to know whether the selected cases and controls resemble the people who will actually be tested.
The STARD 2015 reporting statement presents 30 essential reporting items intended to make diagnostic accuracy studies more complete and transparent. The statement’s abstract, published October 28, 2015, explains that incomplete reporting obstructs critical appraisal and replication. Reporting requirements should not be mistaken for a guarantee that a compliant study is unbiased: readers still need to evaluate the design, the population, and the interpretation.
Consecutive or otherwise systematically selected participants can reduce some selection concerns, but the setting still matters. A tertiary referral clinic receives a different mix from a community service. Exclusion criteria can further narrow the population. The report should make those boundaries explicit and explain who was left out. A diagnostic claim becomes more useful when readers can identify the people it does not yet cover, rather than assuming that every participant represents everyone with a similar symptom.
6. The reference standard has to answer the right question
A new test is evaluated against some definition of the target condition. That reference might be a measurement, a clinical assessment, a combination of procedures, or follow-up information. Its role is crucial: the study's error counts depend on how the reference classifies participants. If the reference is imperfect or addresses a different target, disagreement becomes harder to interpret.
FDA's March 13, 2007 statistical guidance recommends comparison with an appropriate benchmark in the intended-use population and distinguishes accuracy measures from agreement with a non-reference comparator. The guidance also warns against evaluation procedures that favor the new test through the way disagreements are resolved.
Imagine a hypothetical blood test intended to identify a disease process. If the comparator detects a related but not identical biological feature, a disagreement may not be a simple false positive or false negative. The study needs to specify which target is being evaluated. Otherwise, a test can appear inaccurate for failing to match a comparator that was never a complete representation of the intended condition.
This does not mean an imperfect reference makes research impossible. It means the uncertainty must be handled openly. Researchers may need a composite definition, independent adjudication, follow-up, or an analysis that acknowledges reference error. The key is not to call a comparator a gold standard merely because it is familiar. Its strengths, limitations, and relationship to the clinical question are part of the evidence.
7. Verification can depend on the result being verified
Sometimes not everyone in a diagnostic study receives the same reference evaluation. That may happen because the reference procedure is burdensome, expensive, or clinically inappropriate for some participants. The resulting evidence can still be useful, but the selection of who is verified must be considered. If verification depends on the new test's result, the observed error pattern can be distorted.
In a hypothetical study, all positive test results receive definitive follow-up, while negative results receive little or none. Undetected disease among the negative group may remain invisible. The study can then appear to have fewer false negatives than it actually does. Conversely, other verification patterns can distort estimates in different directions. The mechanism matters more than a generic label of bias.
A study report should show how many participants underwent each reference procedure and why. It should explain the handling of those without definitive classification. Treating unverified participants as automatically disease-free would be an assumption, not an observation. Excluding them silently changes the study population.
Statistical methods can sometimes address partial verification under stated assumptions, but they cannot guarantee recovery of truth from any missing-data pattern. The analysis should explain what is assumed about unverified participants and how conclusions change under plausible alternatives. The central question is whether the study had a fair opportunity to discover both kinds of error. A test cannot be credited with ruling out disease simply because the research design stopped looking for disease after a negative result.
8. The new test should not write its own answer key
A reference diagnosis can be influenced by the result of the test being evaluated. If the new test helps determine whether a participant is considered affected, the evaluation risks circularity. Agreement may increase because the answer key partly incorporates the answer being tested.
A hypothetical expert panel might review clinical records to classify participants. If panel members see the new test result and use it in their judgment, the study no longer provides a fully independent comparison. That may reflect ordinary clinical reasoning, but it complicates an estimate of the test's standalone diagnostic performance. The report needs to state what information the panel had and how it was used.
A related problem arises when only disagreements receive additional investigation. If the new test and comparator agree, their shared error may go unnoticed. If they disagree, a resolution procedure may preferentially favor the new method. The resulting revised table can look more accurate than the original evidence justifies.
The solution is not necessarily to deny evaluators every piece of clinical information. The appropriate information depends on the target condition and study design. The requirement is to preserve independence where the performance claim needs it and disclose any incorporation. Readers should be able to tell whether the test was compared with an external judgment or helped create that judgment. A diagnostic study is strongest when the procedure for establishing the target condition is specified before the investigators know which classifications would make the new test look best.
9. A threshold is a decision, not a natural boundary
Many tests produce a continuous measurement that is converted into positive or negative using a cutoff. Moving the cutoff changes the balance between missed cases and false alarms. The chosen threshold therefore encodes a decision about the intended use and the consequences of error, not merely a property of the instrument.
Consider a hypothetical biomarker whose values overlap between affected and unaffected people. A lower cutoff may identify more affected people while also flagging more unaffected people. A higher cutoff may reduce false positives while missing more cases. There may be no single threshold that is best for every setting. A preliminary triage role can justify a different balance from a result used to initiate a consequential intervention.
Threshold selection also creates an evaluation problem. If researchers choose the cutoff that performs best in the same dataset used to report final accuracy, the estimate may be optimistic. The selected boundary has benefited from knowledge of those particular observations. Testing a prespecified threshold in an independent population provides stronger evidence about how it will perform on new people.
The report should distinguish an exploratory cutoff from a validated one. It should state whether the threshold was fixed before analysis and explain its intended clinical role. A receiver operating characteristic curve can summarize performance across thresholds, but the deployed test operates at particular decisions, not across the entire curve at once. A strong overall summary cannot substitute for evaluating the operating point that users will actually encounter.
10. An indeterminate result is a result of the workflow
Not every test returns a clean positive or negative. Some produce an uncertain category; others fail technically or require repetition. Excluding these outcomes from the main performance summary can make the system appear more decisive than it is. The frequency and handling of non-definitive results are part of practical performance.
Suppose a hypothetical study begins with one thousand people. Eight hundred receive an interpretable binary result, while two hundred need further testing. If the eight hundred results are highly accurate, that is useful information. It does not mean the test provides a highly accurate definitive answer for everyone. The missing fifth of the workflow needs its own explanation.
Indeterminate results may be concentrated near the boundary where clinical decisions are most difficult. Removing them can improve reported sensitivity and specificity by excluding hard cases. That may be a legitimate description of performance conditional on a definitive result, provided the condition is explicit. It is misleading if readers infer that the hard cases have been solved rather than deferred.
The next step matters. Does an indeterminate result trigger a repeat sample, another method, specialist review, or no clear action? Each pathway has costs and risks. The test should be evaluated as part of that pathway. An uncertain category can be a responsible design feature when it prevents overconfident classification. Its value depends on a workable response, and its prevalence should be reported rather than buried in exclusions or treated as an inconvenience outside the accuracy calculation.
11. Analytical sensitivity is not clinical sensitivity
A laboratory method may detect very small quantities of an analyte. That is an important analytical capability, but it does not automatically mean the method identifies nearly everyone with a disease. The biological marker may be absent, variable, or unrelated to the target condition in some people. Clinical sensitivity concerns the test's performance in the relevant population, not just its ability to detect material in a sample.
The National Cancer Institute's assay-performance reporting document distinguishes detection and quantitation limits, interference, precision, and comparisons with reference measurements. The NCI document illustrates why a complete assay evaluation includes several different properties. No single laboratory metric establishes all of them.
A hypothetical test might reliably detect a molecule at very low concentration. If that molecule is elevated in only a subset of affected people, the analytical achievement does not guarantee high disease detection. Conversely, a test with an adequate but not record-breaking detection limit could be clinically useful if the relevant signal is well separated in the intended population.
This distinction protects against a common promotional shortcut: describing a more sensitive assay as a better diagnostic test without showing the clinical connection. The improvement may be real and valuable, but the claim needs to identify what became more sensitive. Detecting less material, distinguishing disease more often, and improving patient outcomes are different achievements. A careful report follows the chain between them rather than allowing one word to carry all three meanings.
12. Interference can be invisible in ideal samples
A test is measured in a sample matrix, not in an abstract container holding only the target analyte. Other substances and sample properties can affect the measurement. A method that performs well in carefully prepared material may behave differently in the range of specimens encountered in practice. Analytical validation should therefore address plausible sources of interference relevant to the intended use.
A hypothetical study could establish excellent repeatability using a narrow set of clean samples. That result describes precision under those conditions. It does not establish robustness to every variation in collection, handling, or composition. The clinical evaluation should include the kinds of samples the workflow will actually receive, and the analytical evaluation should explain which challenges were examined.
Interference also complicates interpretation of an unexpected result. A discrepancy might reflect genuine biology, a problem in the new method, an issue with the comparator, or a sample-specific effect. Investigating these possibilities can improve the test, but the investigation should not be selectively used to erase errors from the performance table after the fact.
The useful reporting distinction is between a known limitation, a measured robustness boundary, and an untested condition. Calling a test robust without specifying the tested range can imply more than the data support. Conversely, a clearly described limitation can make a test safer and more useful because users know when another method is needed. The objective is not to promise a test that never encounters difficulty; it is to make predictable difficulties detectable and manageable within the intended pathway.
13. The operator is part of the measurement system
A diagnostic device used by a trained laboratory professional and the same device used in a less controlled setting may not produce identical practical performance. Instructions, specimen collection, timing, interpretation, and error recognition all matter. Evaluating the intended user is therefore part of evaluating the test.
FDA's CLIA-waiver guidance discusses demonstrating accuracy in the hands of users with limited or no laboratory training and considers differences in training, environment, and patient population. The guidance does not imply that untrained users always perform poorly. It establishes why performance demonstrated by experts is not automatically sufficient evidence for another use setting.
Consider a hypothetical device that gives a correct result when every step is performed precisely but allows a common mistake to produce a plausible-looking answer. Its laboratory accuracy may be strong while its real-world reliability is weaker. A design that detects the mistake and returns an error could be safer, even if it produces more invalid results. Counting only successful completed tests would miss that distinction.
Human-factors evidence should therefore examine the complete interaction, not merely whether users can read the final display. A study should reflect the instructions and support available in actual use. Intensive coaching during evaluation can make a workflow look easier than it will be later. The important question is whether the intended users can obtain and understand a reliable result under realistic conditions, including recognizing when the system has not produced a result that should be acted upon.
14. Simple tests are not error-proof tests
Simplicity can reduce opportunities for error, but it does not remove them. CDC's waived-testing page, updated April 2, 2026, states that tests classified as simple and low-risk are not completely error-proof and emphasizes correct performance. The CDC guidance page provides a current institutional reminder that ease of use and freedom from error are different properties.
For a hypothetical testing program, an error can occur before the assay begins, during operation, when the result is recorded, or when it is communicated. A specimen may be mismatched, a result may be attached to the wrong record, or an invalid result may be mistaken for a negative one. The instrument's analytical performance does not measure every one of these risks.
This is why a practical evaluation should follow the result through the workflow. How often is a usable sample obtained? How often is the test completed correctly? How often is the result delivered in time and interpreted within the intended context? These are different failure points, and improving one does not automatically improve the others.
The distinction is especially important in comparisons between centralized and decentralized testing. A less analytically sensitive method that reaches people reliably and quickly may have value in a particular pathway, while a more sophisticated method may be preferable for another purpose. That is an empirical comparison of complete systems, not a reason to dismiss analytical quality. The best system is the one whose evidence fits the clinical task and whose operational limitations are understood.
15. Repeat testing does not always multiply reassurance
It is tempting to assume that two negative results make a missed condition extremely unlikely by multiplying two false-negative probabilities. That calculation requires assumptions about the relationship between the errors. If the same reason causes both tests to miss the condition, the errors may be correlated. Repetition is not automatically equivalent to independent confirmation.
Imagine a hypothetical test that misses cases when the target signal is absent from the sampled material. Repeating the same test immediately on a similar specimen may not overcome that problem. A repeat could be useful for some technical errors while doing little for a systematic limitation. The value depends on why the first test might have been wrong.
The same issue applies to two different tests. Different names do not guarantee independent errors. They may rely on the same underlying biological signal or share a pre-analytical vulnerability. A confirmatory strategy should be evaluated as a strategy rather than assumed to inherit the product of separate accuracy estimates.
Timing can change the relationship as well. A later test may observe a different stage of the condition, so the interpretation is not merely a repeated measurement of an unchanged state. This article does not prescribe repeat-testing schedules. The methodological point is that a sequence of tests has its own performance characteristics. A strong evaluation measures or models those characteristics transparently, including dependencies, rather than borrowing a reassuring arithmetic rule that may not fit the workflow.
16. A small study can produce a perfect-looking percentage
If a study observes no false positives among a small number of unaffected participants, the observed specificity is one hundred percent. That does not establish that the true false-positive rate is zero. The estimate has uncertainty, and a larger study may reveal errors that the smaller one simply had little opportunity to observe.
A hypothetical test evaluated in twenty unaffected people might return twenty negative results. This is compatible with good performance, but it is not strong evidence about very rare errors. A claim intended for a large screening population may depend on distinguishing small false-positive rates, which requires substantially more information than a perfect-looking result in a small convenience sample.
The denominator should therefore accompany the percentage, along with an appropriate uncertainty interval. Readers should resist comparing two tests solely because one reported one hundred percent and another reported ninety-nine percent in a much larger, more representative evaluation. The second study may provide stronger evidence about practical performance despite its less dramatic point estimate.
Uncertainty also applies to subgroup claims. A test can have many participants overall and very few in a subgroup central to the intended use. Reporting the overall result does not resolve the subgroup's performance. The correct response is to identify the limitation and seek additional evidence, not to assume equality or difference without adequate data. Precision is a property of the estimate and study design, not a reward for presenting a percentage with more decimal places.
17. External validation means more than a new random split
Separating development data from evaluation data is important, but the separation must match the intended generalization. A random split of records from the same sites, collection period, and processing workflow may test performance on similar data while leaving uncertainty about new settings. External validation asks whether the test retains useful performance beyond the environment that shaped it.
A hypothetical algorithmic diagnostic test might be developed using archived samples from several hospitals. If related samples from the same people or repeated measurements appear on both sides of a split, the evaluation can be overly favorable. Even without direct overlap, shared site-specific features may make the test's job easier than it will be elsewhere.
A stronger evaluation preserves independence at the relevant level and tests the finalized procedure in a population resembling the intended deployment. That includes the threshold, preprocessing, handling of invalid results, and any clinical information used by the model. Changing those components after seeing the evaluation results turns part of the evaluation back into development.
External validation is not a single permanent certificate. A test can be well supported for one setting and still require evidence for another. Differences in patient spectrum, sample handling, equipment, or clinical pathway can matter. The goal is to define where performance has been demonstrated and where transfer remains an assumption. That clarity is more useful than a broad label of validated attached to a test whose evaluated conditions are difficult to discover.
18. Accuracy does not establish that testing improves outcomes
A test can classify a condition accurately without improving the outcomes that matter to patients. The benefit depends on what happens after the result. If the result does not change management, arrives too late, or triggers an ineffective or harmful response, better classification may not translate into better health.
Consider a hypothetical test that identifies a biological abnormality earlier than existing methods. That is an important detection result. Whether earlier detection helps requires evidence about the available response, the natural history of the abnormality, and the consequences of labeling people sooner. More detected abnormalities are not automatically more prevented harms.
A diagnostic strategy can also change the use of other tests. It may reduce invasive procedures, shorten uncertainty, or direct resources more efficiently. Those are potential benefits that can be measured. It may also create additional follow-up, anxiety, or unnecessary intervention. The evaluation should compare complete pathways rather than assume that every new piece of information is beneficial.
This distinction does not require every early study to demonstrate patient outcomes before the test can be considered promising. Development proceeds through stages. The reporting requirement is to name the stage accurately: analytical performance, diagnostic performance, decision impact, or clinical benefit. Each stage answers a different question. A strong accuracy study should receive credit for what it establishes, while the next-stage claims remain open until they have their own evidence.
19. The result has to survive communication
A technically correct result can become misleading when communicated without context. A positive finding may be described as a diagnosis when it is intended only to support further evaluation. A negative finding may be described as ruling out a condition when the test's scope is narrower. The language on the report and in public coverage can therefore change the practical meaning of the test.
A hypothetical patient-facing summary that says ninety-five percent accurate may sound like a ninety-five percent probability that any individual result is correct. As the earlier examples showed, that interpretation may not follow. Communication should identify the relevant measure and avoid presenting population statistics as a personalized probability without the necessary context.
The report should also make invalid and indeterminate outcomes unmistakable. A blank field, ambiguous symbol, or delayed message can be interpreted incorrectly if the workflow does not explain what it means. The responsibility is not only on the person receiving the result; it is on the system to communicate within the intended use.
For journalism, the most useful questions are often simple: accurate for whom, compared with what, at which threshold, and followed by what action? Those questions can fit into a concise article even when the underlying study is complex. They prevent the promotional number from becoming the whole story. Clear communication does not require reproducing every statistical detail. It requires preserving the distinctions that would materially change a reader's understanding of what the test can establish.
20. A testing program has a capacity constraint
A diagnostic pathway can be limited by what happens after the initial test. If a large number of positive or indeterminate results require a scarce confirmatory procedure, the program's practical performance depends on that capacity. A test may be analytically fast while the complete route to an actionable answer remains slow. Evaluating only the first step can hide the bottleneck.
Return to the hypothetical low-prevalence example with ten thousand people, ninety true positives, and four hundred ninety-five false positives. If every positive result triggers further assessment, the pathway must accommodate five hundred eighty-five people. That is not an argument against testing. It is a concrete workload implied by the assumed performance and prevalence. The resource calculation should be made alongside the accuracy calculation rather than after a program is already overwhelmed.
The relevant comparison may include existing delays and missed cases. A new test could improve access by directing limited confirmatory resources more effectively. It could also divert those resources toward a large number of low-yield referrals. Which outcome occurs depends on the intended population, referral rules, and the alternative pathway. A simplistic count of additional positive results cannot establish success or failure.
Access to follow-up can also change who benefits. If only some people can complete confirmation, the initial test's apparent reach may exceed the reach of the diagnostic service. A study of implementation should examine completion and time to resolution, not only uptake of the first test. Otherwise, a program can report impressive testing volume while leaving many participants with unresolved findings.
These are measurable questions. How many people move through each stage? How long does each stage take? What proportion receives a definitive answer, and what happens to those who do not? A useful evaluation keeps the denominator from the beginning of the pathway, while separately reporting performance among those who complete it. The result is a more realistic account of whether the test expands reliable diagnosis or merely expands the queue for the next step.
21. The setting is where the claim becomes real
A diagnostic test earns confidence through a chain of evidence. The chain should remain visible when a result moves from a research report into a purchasing decision, a service redesign, or a public announcement. The assay must measure reliably; the clinical evaluation must represent the intended population; the reference must address the target condition; and the workflow must deliver an interpretable result that supports an appropriate decision. Weakness at one link can limit the usefulness of strength at another.
The sources discussed here include older methodological guidance and more recent regulatory and operational examples checked in October 2026. Their central lesson is not that new tests are inherently suspect. It is that the most persuasive evidence is specific. A test can be highly useful within a clearly defined role while remaining unproven for a broader one.
When evaluating the next accuracy claim, look first for the intended use and the participant flow. Then identify the denominators behind sensitivity, specificity, and predictive values. Ask how the reference was established, how uncertain results were handled, and whether the operators and samples resemble actual use. Finally, ask what changes after the result and whether that change has been evaluated.
A test does not become less impressive because its boundaries are explained. Those boundaries are what allow clinicians, researchers, and the public to understand its value. The most important question is not whether the number in the headline is large. It is whether the study has shown that the test can do the job being asked of it, for the people who will receive it, in the place where its result will matter.