1. Two significance numbers can describe the same excess
In its analysis of 2015 collision data, ATLAS reported a diphoton excess around 750 GeV. For the spin-zero search, the local significance was 3.9 standard deviations. The global significance was about 2.1 standard deviations after accounting for the search over possible signal locations and widths. These were not competing descriptions from an enthusiast and a skeptic. They appeared in the collaboration's own research record and answered different statistical questions. The manuscript was first submitted June 13, 2016; this is a historical example, not a newly announced particle. ATLAS diphoton search.
The distinction matters whenever a striking feature is selected from a broader search. How surprising is the feature at this specified location? How surprising is it to find a feature at least this striking somewhere in the search? A calculation can answer the first question correctly while leaving the second unanswered.
“Five sigma” is consequently not a complete sentence about a discovery. A significance needs a hypothesis, a definition of what counts as more extreme, a statistical model, and an account of the search that produced the candidate. It does not reveal those ingredients merely by being a large number.
This article follows those ingredients through worked examples. All invented searches, measurements, trial counts, and probability models below are explicitly hypothetical. They are not reconstructions of confidential collider analyses, simulations of ATLAS or CMS, or allegations that any collaboration manipulated its results. The real papers supply bounded examples and methods; the synthetic calculations make the underlying distinctions inspectable.
The aim is not to replace physics with skepticism about every number. Strong evidence deserves to be recognized. The aim is to identify which conclusion the number supports, which choices preceded it, and what further evidence is needed before a localized excess becomes a convincing account of a new physical process.
The search history is part of that evidence. A mass chosen before examining the relevant data is not equivalent to a mass chosen because it contained the largest bump. A fixed selection rule is not equivalent to the most attractive result among many revised rules. Independent measurements are not equivalent to repeated plots of the same events. These differences are scientific inputs, not presentation details to be removed for a cleaner headline.
2. The probability runs in a particular direction
The Particle Data Group's 2026 Statistics review defines a p-value as a probability calculated under a specified hypothesis for outcomes at least as incompatible with that hypothesis as the observed outcome. It explicitly distinguishes that quantity from the probability that the hypothesis itself is true. For a positive-signal search using the conventional one-sided Gaussian-equivalent scale, five sigma corresponds to a tail probability of about 2.87 times ten to the minus seven. The review was revised in June 2025; the edition date is not a new experimental result. PDG 2026, Statistics.
To make the direction concrete, imagine a machine that produces observations according to a completely specified background model. A rule assigns each possible observation a score. Before collecting data, the analyst defines which high scores would count as unusual. The p-value asks how often the background model would produce a score at least as extreme as the one eventually observed. It does not first assign probabilities to competing explanations and then update them.
A separate hypothetical decision exercise shows why the distinction matters. Suppose a screening procedure has a false-positive rate of one in a thousand and detects 80 percent of genuine signals. Those are assumed properties of a fixed procedure, not the observed p-value of one dataset. Apply it to a fictional population of one million cases in which exactly 1,000 contain a signal. In expectation, 800 genuine signals and 999 background cases trigger the procedure. Among the expected 1,799 triggers, about 44.47 percent come from genuine signals.
Now apply the same procedure to another invented population in which 100,000 of the million cases contain signals. The expected counts become 80,000 genuine triggers and 900 background triggers. The expected genuine fraction among triggers is about 98.89 percent. The procedure's assumed false-positive rate and sensitivity have not changed. The population composition has.
This is a teaching model, not an assignment of prior odds to particle theories. It demonstrates that a false-positive rate cannot, by itself, determine the probability that a triggered case contains a signal. An observed p-value supplies even less of that missing structure: it is not automatically the false-positive rate of a prechosen decision rule, and it is not a likelihood ratio between two fully specified theories.
The practical consequence is a wording discipline. “The background model rarely produces a result this extreme under this procedure” is a conditional statistical statement. “There is only this probability that the claimed particle does not exist” is a different statement requiring additional assumptions and analysis. Replacing the first with the second does not make a result easier to understand; it changes what has been calculated.
3. Searching twenty places changes the question
Gross and Vitells' work on the look-elsewhere effect addresses a resonance whose location is not fixed in advance. The relevant search-level question concerns an excess anywhere in the specified range, rather than only the position selected afterward. Their paper develops an approximation for that problem; the elementary examples here use independently specified probability models instead of reproducing their approximation. Trial factors for the look-elsewhere effect.
Imagine twenty independent tests of background-only data. Each test has a probability of 0.002 of producing an outcome at least as extreme as a specified threshold. The chance that one test does not cross the threshold is 0.998. Because the tests are independent in this hypothetical model, the chance that none crosses is 0.998 raised to the twentieth power. The chance that at least one crosses is one minus that quantity, approximately 3.925 percent.
The local tail probability was 0.2 percent. The probability for at least one qualifying result in the twenty-test search is nearly twenty times larger. Nothing happened to the observed data between those statements. The event being evaluated changed from one designated test to the most extreme result among twenty opportunities.
A more dramatic example uses 1,000 independent tests, each with a threshold-crossing probability of 0.001. The probability of at least one crossing is approximately 63.23 percent. A result that sounds unusual when described as “one in a thousand at this location” is unsurprising if the procedure gives itself a thousand independent chances to find one.
Neither calculation says that every search uses independent tests or that a particle-physics trial factor is simply the number of plotted points. Those assumptions belong only to the examples. Their purpose is to show why the search cannot be reconstructed solely from the location of the final peak.
Suppose an analyst instead announces in advance that only the seventh test will determine the result. If that commitment is genuine and the other tests do not influence the selection or interpretation of the seventh, the relevant event can be different. The issue is not whether twenty measurements physically exist; it is what procedure turns them into the reported claim.
Conversely, writing down the seventh test after learning that it is the most unusual does not retroactively make it preselected. The original opportunities still existed. A record of the search plan, including the statistic and selection rule, makes this difference checkable rather than dependent on an analyst's later recollection.
The correction is therefore not a punishment for curiosity. Broad searches are scientifically valuable precisely because they can find things whose location was not predicted. Their significance calculation must simply describe that broader opportunity. A local result can still be reported, provided its scope is clear and it is not silently substituted for the search-level result.
4. A thousand plotted points are not necessarily a thousand independent trials
The independent-test examples are easy to calculate, but real searches often inspect related candidates. Adjacent windows can contain many of the same events. Nearby signal hypotheses can produce similar fitted outcomes. Treating every point on a finely drawn curve as independent would mistake display resolution for independent evidence.
Consider an exact synthetic construction. Begin with ten independent tests, each having probability 0.002 of crossing the threshold. Then display every test twice under two different labels, without changing the data or calculation. The plot now contains twenty labeled points, but the probability of at least one crossing is still one minus 0.998 to the tenth power, approximately 1.982 percent. Duplicating a result does not create a new opportunity for a fluctuation.
Compare that with the genuinely independent twenty-test example, whose probability was about 3.925 percent. Both displays contain twenty points. Their search-level probabilities differ because their dependence structures differ. Counting labels cannot resolve the distinction.
Now imagine a continuum between those extremes: overlapping windows that are neither independent nor exact copies. The correct search-level probability depends on their joint behaviour under the background model. It cannot be obtained by choosing whichever of the two extreme calculations produces a preferred conclusion. Nor can a visually smooth curve establish how much dependence is present.
A conservative bound can sometimes make a limited statement without independence. If twenty events each have probability at most 0.002, the probability that at least one occurs is at most their sum, or 0.04. This union bound is not an assertion that the probability equals four percent. It may be loose, especially when the events overlap substantially.
The distinction between a bound and an estimate is important in reporting. A safe upper bound can support a cautious conclusion without identifying the exact probability. An exact calculation within a simplified independent model can be precise but inappropriate for a correlated search. The most decimal places do not necessarily identify the most defensible answer.
A useful search description therefore explains what was varied: candidate mass, assumed width, final state, event selection, or another feature. It also states how their dependence was included in calibration. It should not merely list how many dots were drawn. The goal is to reproduce the set of opportunities that could have produced the reported candidate, not to count pixels.
This point also limits retrospective arithmetic by outside commentators. Multiplying a published local p-value by an arbitrary number of mass bins is not automatically a valid global correction. A reader can identify missing information and ask for the search definition without pretending that a rough count reconstructs a collaboration's full statistical analysis.
5. Exploration is useful; it is not confirmation by renaming
Junk and Lyons describe blind-analysis methods used to reduce the influence of desired outcomes on analysis choices. They discuss freezing a procedure after using a designated exploratory subset and then applying it to still-blinded data. The distinction is about what information influenced the choices, not whether researchers were curious or worked hard. Reproducibility and Replication of Experimental Particle Physics Results, blind-analysis section.
Imagine a fictional project called Aurora Search. Before opening its designated test data, the team records a mass interval, three candidate widths, an event-selection rule, a background model, and the statistic that will identify its leading candidate. It also records which calibration samples may be examined while developing the procedure. These details define the starting analysis; the name Aurora refers to no real experiment.
The team first examines an explicitly exploratory dataset. A promising feature appears near one end of the interval. An analyst discovers that tightening an event-selection threshold makes the feature more pronounced. That may be an excellent lead. It is not yet independent evidence that the tightened selection reveals a new process.
There are several legitimate next steps. The team can treat the result as exploratory and seek new data. It can evaluate a revised, fully specified procedure with a calibration that includes its selection process where feasible. It can investigate whether the feature reflects a detector or modelling issue. What it cannot do honestly is describe the already-inspected sample as if it had remained untouched by the choices.
Suppose the team freezes the revised rule and applies it to a fresh dataset. That new analysis has a different evidential role. It asks whether the specific feature or prediction survives a test whose outcome did not select the rule. It does not erase the exploratory history; it adds a new observation with a better-defined relation to that history.
A dated analysis record can make these transitions clear. Version A contains the initial selection. Version B contains the change prompted by exploration. Version C freezes the procedure for the fresh sample. The record identifies which data informed each version. A later reader can then distinguish development from evaluation instead of inferring everything from the last version's polished description.
A practical complication is that a “fresh” dataset may share calibrations, reconstruction software, or background assumptions with the earlier analysis. New events reduce one kind of dependence, but they do not automatically eliminate every shared source of error. The investigation must identify which uncertainties are genuinely new and which persist.
This is not an argument for forbidding changes after an unexpected result. An unexpected result is often exactly why a method should be examined. The distinction is between making a change transparently and pretending the changed method was the original test. Exploration becomes stronger science when its history is retained, not when its exploratory character is concealed.
6. An uncertain background is not a known constant
Cowan, Cranmer, Gross, and Vitells formulate likelihood-based searches in which quantities such as background rates and calibration effects enter as nuisance parameters. Auxiliary measurements can constrain them, but treating their measured estimates as exact would discard part of the uncertainty. Their asymptotic formulae also have stated conditions; a convenient approximation is not automatically valid for every sample. Asymptotic formulae for likelihood-based tests of new physics.
Use a deliberately simple Gaussian measurement model to see the effect. Let Y be a signal-region measurement with standard deviation ten units. Let B be an independent background-reference measurement, also with standard deviation ten units. Under the fictional no-signal hypothesis, both have the same unknown mean. Suppose the observed values are Y equals 120 and B equals 100.
If B were incorrectly treated as an exactly known background value, dividing the difference of twenty by Y's standard deviation of ten would give a score of two. But in the stated model B is itself measured with uncertainty. The difference Y minus B has variance 100 plus 100, or 200, because the measurements are independent. Its standard deviation is about 14.14. The standardized difference is therefore about 1.414, not two.
This example is not a fit to collision counts, and it does not assert that every nuisance parameter can be handled by adding variances. Its variables are explicitly Gaussian measurements with known standard deviations and the stated independence. It shows what changes when one of the assumed inputs is an estimate rather than a constant.
Now alter the design: suppose the reference is the average of four independent measurements, each with standard deviation ten. Its standard deviation becomes five. The difference then has variance 100 plus 25, giving a standardized score of about 1.789. More reference information improves the comparison, but it still does not make the reference perfectly known.
If the signal-region and reference measurements share a calibration error, the covariance must also be considered. The variance of their difference includes minus twice their covariance. A common offset may partly cancel, while a differently coupled uncertainty may not. The physical measurement model determines the relationship; attaching the same percentage uncertainty to two quantities does not by itself specify their correlation.
The reporting question is therefore not simply whether a paper mentions “systematics.” It is which quantities were uncertain, what observations constrained them, what dependence was assumed, and how those assumptions affected the result. A small statistical tail probability cannot certify the adequacy of inputs that were treated as certain without justification.
A sensitivity study can be useful here without being a search for a desired answer. It can identify which plausible model changes materially affect the inference and which do not. The alternatives should be motivated and documented. Trying arbitrary backgrounds until a preferred significance appears would introduce a different selection problem rather than solve the original uncertainty problem.
7. The calibration must describe the procedure that produced the result
Cranmer's practical statistics lectures distinguish the probability model from the tests applied to it and describe how auxiliary observations can inform that model. This distinction is easy to lose when a significance appears as the final output of software: the calculation is conditional on the model supplied to the program. A successful numerical evaluation does not demonstrate that the model describes the apparatus. Practical Statistics for the LHC.
Consider a synthetic score X that is assumed to follow a standard normal distribution under background only. The decision rule flags X greater than or equal to five. Under that assumed model, the probability is approximately 0.0000002867. Now suppose the actual background score remains Gaussian with mean zero, but its standard deviation is 1.2 rather than one. The threshold is unchanged at X equals five; in units of the actual standard deviation, it is about 4.167.
The actual threshold-crossing probability in this altered model is approximately 0.00001545, about 54 times the probability calculated from the narrower model. These are exact-model numerical calculations, not measurements of a collider or an estimate of how often particle discoveries are wrong. They show why a modest error in a distribution's width can matter greatly far out in its tail.
The example does not imply that experimental background models are always Gaussian or that a universal twenty-percent inflation fixes every systematic uncertainty. A misspecified mean, a rare additional component, or dependence between measurements could have different consequences. The point is that an impressive tail probability cannot validate the distribution used to calculate it.
The same requirement applies to the selection procedure. Suppose the fictional Aurora Search calibrates the maximum score over its original mass interval but then reports the best outcome after also trying several event selections. If those additional choices can change the reported maximum, calibration of the original procedure does not automatically describe the expanded one. The program may be computing its assigned task correctly while the scientific claim refers to a different task.
A useful validation exercise records the inputs and choices made available to the analysis, then asks what output that entire procedure would produce under the stated background model. Which settings were fixed? Which were fitted? Which were selected after looking? Which auxiliary data were included? The answers define the object being calibrated.
Numerical reproducibility and scientific adequacy are distinct checks. Re-running the same model and code can reproduce the same significance while leaving an omitted uncertainty untouched. Changing the code without tracking the model version can create the opposite problem: a different result with no clear explanation of what changed. Neither problem is resolved by reporting more digits.
The most useful conclusion from a calibration check is specific. Perhaps the calculation matches the intended search, but a tail model remains uncertain. Perhaps the model is adequate for one region but not another. Perhaps an implementation bug changes the output. These are different findings, requiring different responses. Treating them all as either “the statistics worked” or “the discovery failed” discards information the analysis needs.
8. Expected significance is a forecast under an alternative, not a second observation
The CMS discovery paper first submitted July 31, 2012 reported an observed local significance of 5.0 standard deviations near 125 GeV. It also reported an expected significance of 5.8 standard deviations for a Standard Model Higgs boson at that mass. The two figures were not two measurements of the same dataset's surprise, and their difference was not evidence of an inconsistency by itself. CMS, Observation of a new boson.
An expected significance describes performance under an assumed signal model and experimental setup. It might be a median or another summary over hypothetical repeated data. An observed significance describes the actual collected data through the chosen test. A report should identify which summary is meant rather than assume that “expected” always means the same statistical quantity.
A fictional forecasting exercise helps separate them. An analysis team specifies a signal strength, a background model, a data-taking plan, and a fixed test. It then calculates how the test would behave if that signal model were true. In one invented set of 1,000 hypothetical repetitions, 700 exceed the chosen discovery threshold and 300 do not. The 70 percent crossing fraction would describe the procedure's power at that particular signal model, not the probability that a real observed excess is a signal.
The exercise is not an actual Monte Carlo result; the counts are stipulated to illustrate the definition. Change the assumed signal strength or experimental exposure and the forecast can change. That does not mean the analyst is allowed to replace the observed result with whichever forecast is most attractive. The forecast and the observation occupy different columns in the record.
Suppose the eventual observation falls below the forecast's median. That can occur even when the assumed signal is present, because a median divides the repeated-outcome distribution rather than guaranteeing a minimum result. Conversely, an observation above the median does not automatically establish a stronger physical signal; it may reflect fluctuation, a parameter difference, or a model problem that needs examination.
The distinction is particularly important for proposed instruments. A sensitivity projection can show that a design would be capable of testing an interesting hypothesis under stated conditions. It is not an observation of the hypothesized process. Describing projected five-sigma sensitivity as a five-sigma discovery would replace a future conditional calculation with an event that has not happened.
For a completed experiment, expected and observed results are valuable together. They help readers understand whether the experiment had a realistic chance to see the proposed signal and whether an apparent absence is informative. But interpreting a discrepancy requires the predicted distribution and assumptions, not merely subtraction of two sigma values.
A concise description can preserve the distinction: the observed result was a specified significance, while the design's expected sensitivity under a named signal model was another. That sentence gives the reader both quantities without pretending that an expectation is a second independent confirmation.
9. Independent evidence requires more than another plot
The ATLAS paper first submitted July 31, 2012 reported a new neutral boson and a significance of 5.9 standard deviations, with properties then compatible with the Standard Model Higgs boson. The separate CMS paper reported its own observation. These were collaboration-specific records, not two websites reproducing one underlying analysis. Their scientific relationship cannot be reduced to adding the displayed sigma values. ATLAS observation paper; CMS observation paper.
Junk and Lyons emphasize that independent confirmation requires attention to overlapping data and shared systematic errors. Different apparatus or collaborations can provide important independence while still sharing some theoretical or calibration assumptions. New data from the same experiment can change statistical fluctuations without removing all earlier systematic uncertainties. Reproducibility and Replication, independent-confirmation discussion.
To illustrate the distinction without assigning a numerical combination to the real papers, consider two fictional analyses with 1,000 selected events each. Suppose 700 events appear in both selections. Calling the pair “2,000 independent events” would double-count the overlap. The union contains 1,300 distinct events. Even that number does not fully specify the dependence of the two test statistics, because the analyses may weight or transform the events differently.
Now suppose the selections share no events but both rely on the same uncertain background-normalization input. Their event-count fluctuations might be independent under a model, while their inferred signal strengths still share an uncertainty. A combination must represent that common input rather than count it twice as independent evidence.
The opposite mistake is to demand absolute independence from every conceivable assumption before acknowledging corroboration. Two experiments can have meaningfully different detector designs, reconstruction methods, and data even if they use common physics theory. The appropriate question is which failure modes are shared and which are independently tested.
A simple measurement example shows why correlation matters. Let two estimates of the same quantity each have variance one in arbitrary units. If independent, their equally weighted average has variance one-half. If perfectly correlated and equal in their fluctuations, the average has variance one. Averaging two labels for the same fluctuation does not halve its uncertainty. Intermediate correlation produces an intermediate variance.
This calculation concerns a stipulated Gaussian-style measurement model, not a formula for combining particle-discovery p-values. A legitimate statistical combination must use the relevant likelihoods or another justified joint procedure. Neither adding sigma values nor multiplying arbitrary published p-values automatically supplies that procedure.
For readers, the most informative follow-up is therefore a map of evidence: which observations are new, which datasets overlap, which uncertainty sources are common, and which predictions are tested in different ways. A second article repeating the first result is publicity. A second analysis with clearly different vulnerabilities can be corroboration. The difference is in the evidence, not the number of headlines.
10. Follow the candidate into later data without rewriting the earlier record
ATLAS's subsequent high-mass diphoton search used 2015 and 2016 data totalling 36.7 inverse femtobarns. Its manuscript, first submitted July 13, 2017, reported no significant deviation from the Standard Model in that search. This is the later research record relevant to the earlier diphoton excitement, not a claim that the 2016 local-significance calculation never existed. ATLAS, later high-mass diphoton search.
A historical account should retain both records: the earlier excess with its stated local and global significance, and the later analysis with additional data and its stated conclusion. It should not turn an exploratory excess into an announced discovery merely to make its disappearance more dramatic. Nor should it suppress the earlier result because the later one was less exciting.
In the fictional Aurora Search, imagine that Version A reports a candidate and Version B processes a larger dataset. To compare them, the record needs more than the two leading sigma values. It needs the data periods, selections, reconstruction versions, signal assumptions, background treatment, and search ranges. A change in significance can reflect several changes at once.
Suppose a reprocessing step changes the measured position of one candidate event. The correct response is to identify the changed reconstruction and show how it affects the analysis. It is not to leave the old event value in one plot and combine it with the new fit elsewhere. Version tracking is part of scientific interpretation, not merely software administration.
Suppose instead that the procedure remains fixed and the new data contain no comparable excess. The evidential question is whether the new observation is compatible with the previously suggested signal and its uncertainty. A disappointing fluctuation can reduce support without establishing that every model in a broad theory family has been excluded. The strength of the conclusion depends on the analysis's sensitivity to the proposed alternative.
That sensitivity matters because absence and exclusion are not synonyms. If an instrument had little chance of detecting a particular signal, failing to see it says relatively little about that signal. If a well-specified model predicts a strong feature that an adequately sensitive test does not find, the result can be much more restrictive. The underlying prediction is what connects the observation to the exclusion.
A responsible update therefore explains what changed and which earlier interpretations remain viable. It can say that a previously interesting candidate did not receive support from a specified later analysis. It should not claim that the later study proves nature contains no unknown particles, or that a background fluctuation demonstrates incompetence by the researchers who reported it cautiously.
Keeping the chronology intact also preserves the value of null results. They constrain interpretations, improve methods, and prevent an intriguing lead from becoming permanent folklore. The scientific record is stronger when a candidate's subsequent tests are as easy to find as its first striking plot.
11. A discovery threshold does not identify the complete mechanism
Louis Lyons' discussion of the five-sigma convention argues that the credibility of a discovery cannot be separated from matters such as systematic uncertainty and the character of the claim. This is a methodological argument by an identified physicist, not a replacement rule adopted universally by every experiment. It helps explain why a numerical threshold is a convention used within scientific reasoning rather than a mechanical certificate of truth. Discovering the Significance of 5 Sigma.
Imagine that a fictional dataset strongly rejects one background-only model. Three alternatives remain under consideration: a new narrow resonance, a different known-process contribution omitted from the model, and an instrumental response not captured by the calibration. A small background-only p-value does not, by itself, assign probabilities among those alternatives. Each requires predictions that can be compared with observations.
Suppose the new-resonance hypothesis predicts the same mass in two decay channels with a specified relationship between their rates. That creates additional tests. Agreement in one channel is not yet the whole prediction. The second channel may strengthen the interpretation, challenge it, or be too insensitive to help. The conclusion follows from the actual pattern and uncertainty, not from requiring every plot to look equally dramatic.
Different physical models can also predict similar features in the initially observed distribution. Establishing an excess is then one step; measuring its properties sufficiently well to distinguish the models is another. A discovery report can legitimately be more cautious about identity than about the presence of an unexpected process.
The distinction is not unique to exotic theories. Even a familiar signal can require separate measurements of its rate, mass, spin-related behaviour, or interactions. A significance for rejecting one null hypothesis does not automatically measure all those quantities. Parameter estimates and uncertainty intervals answer questions that a discovery p-value was not designed to answer.
An invented reporting example makes this concrete. “A localized excess inconsistent with the specified background model” describes an observation and test. “The excess is compatible with Model A” adds a comparison. “Model A is established and every competitor is excluded” requires much more. Those statements should not be treated as interchangeable merely because the first has crossed a conventional threshold.
The standard also applies to extraordinary explanations advanced outside collaborations. A statistical anomaly does not establish a portal, an undisclosed technology, or a particular cosmological story unless that explanation makes relevant testable predictions and fits the evidence. Refusing the unsupported leap is not refusing to investigate the anomaly.
The productive next question is which observation would distinguish the remaining explanations. A different channel, a different detector response, a control measurement, or additional data may be informative. Repeating the original significance more emphatically does not supply the missing discriminating test.
12. Read the search as a sequence of decisions
A particle search begins before the most striking plot exists. Someone chooses what data to collect, which events to retain, which models to compare, what parameters to vary, and what statistic to report. Some choices are fixed by theory or instrument design; others are learned through calibration and exploration. The final number compresses that sequence. Understanding it requires recovering the parts relevant to the claim.
The useful questions are concrete. Was the reported location fixed before examining the relevant dataset? What range and alternatives were actually searched? Which choices were optimized using the same events? What background and uncertainty model calibrated the result? What observations, beyond the leading excess, test the proposed explanation? These questions are not accusations. They identify the experiment that the probability statement is supposed to describe.
The synthetic examples show why the answers matter. Twenty independent opportunities produced a different threshold-crossing probability from twenty labels representing only ten distinct opportunities. An uncertain reference changed the standardized comparison. A wider background-score distribution changed the tail probability dramatically. Expected sensitivity did not become observed evidence. Overlapping events did not become independent merely because two analyses plotted them.
A well-written discovery account need not burden every sentence with all these qualifications. It should attach the essential scope to the key claim and make the methodological record accessible. Local and global significance can be reported together. Measured results and expected sensitivity can occupy separate sentences. Exploratory choices can be acknowledged without dismissing the resulting scientific lead.
The same discipline improves criticism. It is reasonable to ask whether a global probability covers the actual search, whether a nuisance model is supported, or whether a later dataset confirms an earlier candidate. It is not reasonable to declare every broad search invalid because it looked in many places, or every result uncertain because its model has assumptions. Science proceeds by testing and constraining assumptions, not by pretending they can be eliminated.
Five sigma remains a stringent conventional benchmark under its stated definition. What it does not supply is the history of selection, the adequacy of the background model, the independence of corroborating evidence, or a complete physical interpretation. Those are not optional decorations added after the statistic. They are the reasoning that connects a statistic to a discovery claim.
The central distinction is therefore not between trusting a large number and distrusting it. It is between a number whose question is understood and a number whose question has been lost. Read the hypothesis, the search, the calibration, and the later tests. Then the significance can do its proper job: quantify a specific piece of evidence without being asked to stand in for the entire scientific case.