Machine Learning Engineer Interview Questions — Statistics & Probability

Start with a question the interviewer will respect: outlier relative to what? A ₹40,000 monthly electricity bill is absurd for a two-bedroom flat and unremarkable for a cold-storage unit. Without a stated population, “outlier” has no meaning.

Two rules, and they disagree in a specific way.

The IQR rule uses quartiles. With Q1 = ₹1,200 and Q3 = ₹2,400, the IQR is ₹1,200, so the fences sit at 1,200 − 1,800 = −₹600 and 2,400 + 1,800 = ₹4,200. Anything above ₹4,200 is flagged.

The z-score rule uses the mean and standard deviation, flagging anything beyond roughly three standard deviations. The problem is circularity: a handful of extreme bills pull the mean up and inflate the standard deviation, which widens the threshold, which lets those very values pass. Quartiles barely move when the tails are extreme, which is why IQR is the more robust choice for detection.

The 1.5 multiplier is a convention from symmetric distributions, not a law. On a strongly right-skewed quantity like electricity billing, it flags a large chunk of the legitimate upper tail. On skewed data, work on a log scale, or use raw percentile cut-offs such as the 1st and 99th.

What to do with what you find is a separate decision, and interviewers listen for whether you treat it as one. A bill of ₹0 is a meter error and should be corrected or excluded. A bill of ₹38,000 from an industrial connection wrongly sitting in a residential dataset is a population problem, not an outlier problem. A genuinely large bill from a large house is real, and deleting it teaches your analysis that such houses do not exist.

If a rule flags 8% of your rows, the rule is wrong for that distribution.

Population parameters describe every unit you care about; sample statistics estimate them from a subset. The correction exists because one of those estimates gets reused.

Take four tea estates sampled from a district, with yields in quintals per hectare:

18  22  26  34

The sample mean is 25. Squared deviations from 25: 49, 9, 1, 81, summing to 140.

Divide by n = 4 and you get 35. Divide by n − 1 = 3 and you get 46.7.

Here is why the second is right. If the true district mean were, say, 27, the squared deviations from 27 would sum to 81 + 25 + 1 + 49 = 156, larger than 140. That is not a coincidence about this example. The sample mean is, by definition, the value that minimises the sum of squared deviations for your particular sample. Any other value, including the true population mean, gives a larger sum. So deviations measured from the sample mean are always at least slightly too small, and dividing by n understates the variance systematically.

Degrees of freedom is the other way to say it. Once you know the mean and any three of the four values, the fourth is determined. Only three deviations are free to vary, so you divide by three.

The correction matters when n is small and fades fast. At n = 5, the difference is 25%. At n = 500, it is 0.2%, which nobody will notice.

One honest caveat interviewers appreciate: dividing by n − 1 gives an unbiased estimate of the variance, but taking the square root of it does not give an unbiased estimate of the standard deviation, because the square root is not a linear operation. Almost everyone uses it anyway, and the residual bias is small.

If you genuinely have the whole population, divide by n.

These are confused constantly, and the confusion is worth clearing with numbers.

A machine on a production line produces a component. Event A is that it fails a dimensional check, with P(A) = 0.05. Event B is that it fails a surface finish check, with P(B) = 0.08.

Mutually exclusive would mean a component can fail one check or the other but never both. Then P(A and B) = 0.

Independent means failing the dimensional check tells you nothing about the surface finish. Then P(A and B) = 0.05 × 0.08 = 0.004, which is not zero.

Notice they cannot both hold. If the events are mutually exclusive, knowing A occurred tells you B definitely did not, which is a very strong dependence. So for events with non-zero probability, mutual exclusivity implies dependence. That is the point an interviewer is usually driving at.

Mutually exclusive is a statement about whether outcomes overlap. Independent is a statement about whether one carries information about the other.

The rules follow from that. For mutually exclusive events, P(A or B) = P(A) + P(B). Otherwise you must subtract the overlap: P(A or B) = P(A) + P(B) − P(A and B). Add 0.05 and 0.08 without subtracting when the events can co-occur, and you have double-counted the components that failed both.

For independent events, P(A and B) = P(A) × P(B). Multiply probabilities that are not independent and the answer is wrong, usually badly. If a batch runs hot, both checks are more likely to fail together, so the true joint probability might be 0.02 rather than 0.004 — five times what independence predicted.

The practical check: compare the observed joint frequency against the product of the marginals. If they differ materially, the events are not independent, whatever the process design claims.

Conditioning means changing what you are dividing by.

A bank reviews 10,000 loan applications. 2,000 come from applicants with no formal credit history. Of those 2,000, 300 eventually default. Across all applications, 700 default in total.

The unconditional default rate is 700 / 10,000 = 7%.

The default rate given no credit history is 300 / 2,000 = 15%.

Nothing about the data changed. You restricted attention to a subgroup, so the denominator shrank from 10,000 to 2,000 and only the defaults inside that subgroup count in the numerator. That is all conditioning is.

Written out:

P(default | no history) = P(default AND no history) / P(no history)
                        = 0.03 / 0.20 = 0.15

Multiply both sides by P(no history) and you have the multiplication rule:

P(A AND B) = P(B) × P(A | B)

That rule is how you chain events. The probability that a randomly picked application has no credit history and defaults is 0.20 × 0.15 = 0.03, matching the 300 out of 10,000 you started with.

Two things worth stating in the room.

P(A given B) and P(B given A) are different quantities and confusing them is one of the most consequential errors in applied statistics. Here, P(default | no history) is 15%, while P(no history | default) is 300 / 700 = 43%. Both are correct and they answer completely different questions.

And when A and B are independent, P(A given B) reduces to P(A), so the multiplication rule collapses to the familiar product. Independence is the special case, not the default assumption.

Sampling without replacement is the everyday example where conditioning is unavoidable, since the second draw’s probabilities depend on what the first draw removed.

Work it with a concrete population rather than the formula. Imagine 100,000 people screened for a rare condition.

Prevalence is 1 in 1,000, so 100 people actually have it and 99,900 do not.

The test catches 99% of the sick: 99 true positives, and 1 missed.

The test correctly clears 99% of the healthy, so it wrongly flags 1%: 1% of 99,900 is 999 false positives.

Total positives: 99 + 999 = 1,098. Of those, only 99 are genuinely ill.

P(disease | positive) = 99 / 1,098 = 0.090

About 9%. Ninety-one out of every hundred people receiving a positive result do not have the condition.

Nothing is wrong with the test. The arithmetic is driven by the base rate: the healthy group is a thousand times larger, so even a small error rate applied to it produces far more false positives than the small sick group produces true positives.

Bayes’ theorem is just this bookkeeping written compactly:

P(D|+) = P(+|D) × P(D) / P(+)

The piece people drop is P(D), the prior. Reading “99% accurate” as “99% chance I have it” is confusing P(positive | disease) with P(disease | positive), and those differ by a factor of ten here.

Two things that follow. Screening a general population for a rare condition produces mostly false alarms, which is why confirmatory testing exists and why mass screening programmes are designed carefully rather than run on everyone. And raising the prior changes everything: test only people with symptoms, where prevalence might be 20% instead of 0.1%, and the same test gives a positive predictive value above 96%.

The same trap appears in fraud alerts, security scanning and rare-event prediction generally. Any rare-event classifier evaluated on accuracy alone will look excellent and be nearly useless.

A cement bagging line fills bags with a mean weight of 50.0 kg and a standard deviation of 0.4 kg, and the process is approximately normal.

So a bag under 48.8 kg happens roughly 15 times in 10,000, since 0.3% falls outside three standard deviations and half of that is on the low side. That number turns a vague worry about underfilling into a rate you can put against a regulatory limit.

The z-score generalises it. A bag at 50.9 kg is (50.9 − 50.0) / 0.4 = 2.25 standard deviations above the mean, which lets you compare it against any other normally distributed quantity regardless of units.

Two corrections worth making unprompted.

The normal distribution is a model, not a property real data possesses. Bag weights are approximately normal because many small independent factors add up in the filling mechanism. Quantities that cannot go below zero and have a long upper tail, such as claim sizes or waiting times, are not normal and the empirical rule badly understates their extremes.

And “95%” is a rounding of 1.96 standard deviations, not exactly 2. It matters when you are constructing intervals rather than describing data.

The failure this prevents: applying three-sigma control limits to a right-skewed quantity. The rule predicts 0.15% of points above the upper limit; on a skewed distribution you might see 3%, and the operators learn to ignore the alarm.

Check the shape before applying the rule. A histogram plus a Q-Q plot tells you more than any single test.

The misstatement is everywhere, so state it carefully: the CLT is about the distribution of a statistic across hypothetical repeated samples, not about the distribution of your observations.

Daily order values on a food ordering platform are heavily right-skewed. Most orders are ₹200 to ₹500, a few are ₹4,000, and the histogram has a long tail. That histogram never becomes normal no matter how much data you collect. Collect a crore orders and it is still right-skewed, just better resolved.

What does become normal is this: take a sample of 200 orders and compute the mean. Do it again with a different 200, and again, thousands of times. Plot those means. That distribution is approximately normal and centred on the true population mean, with standard deviation:

SE = sigma / sqrt(n)

If the population standard deviation is ₹600, the standard error at n = 200 is 600 / 14.14 = ₹42.4. So sample means cluster within roughly ±₹85 of the truth about 95% of the time, even though individual orders scatter far more widely.

This is why a t-test on skewed data at large n is defensible. The test needs the sampling distribution of the mean to be approximately normal, not the data.

Three conditions people skip.

Observations must be independent and identically distributed. Clustered data, such as several orders from the same household, breaks it and the effective sample size is smaller than the row count.

The population needs finite variance. Genuinely heavy-tailed quantities where variance is undefined do not obey the standard CLT.

And “n = 30 is enough” is a rule of thumb, not a theorem. For mild skew, 30 is fine. For the order-value distribution above, you might need several hundred before the sampling distribution looks convincingly normal. The heavier the skew, the larger n has to be.

A state education department wants to estimate average learning outcomes across 12,000 schools.

Simple random. Draw 400 schools at random from the full list. Unbiased and simple, but the surveyors travel to 400 scattered locations, and by chance you might get very few schools from one region.

Stratified. Divide schools into strata by type or region, then sample within each proportionally. If outcomes differ substantially between government and private schools, this is materially more precise than simple random at the same sample size, because you have eliminated the between-stratum variation from your sampling error. It also guarantees every stratum appears, which simple random does not.

Cluster. Pick 40 districts at random and survey every school in them. Far cheaper, since travel collapses. The cost is precision: schools within a district resemble each other, so 400 schools from 40 districts carry less information than 400 scattered schools. The effective sample size can be a fraction of the nominal one, and treating it as 400 independent observations makes your confidence interval too narrow.

Systematic. Sort the list and take every 30th school. Easy to execute and usually fine. It fails when the ordering has a cycle matching your interval. Sample every 7th day of transactions and you get the same weekday every time, which is a real and well-documented way to produce a badly biased sample from a procedure that looks rigorous.

The trade-off to state plainly: stratification buys precision when strata differ; clustering buys cost savings and pays in precision. Choose based on whether budget or accuracy is the binding constraint.

What none of these fix is non-response and coverage bias. If the sampling frame omits unregistered schools, or if the schools that decline to participate differ systematically from those that agree, a perfect sampling method still gives a biased estimate. That is the failure worth flagging, because it survives every technical improvement to the sampling design.

A gym chain surveys members about satisfaction and finds 84% rate it highly. The survey went out by email to members who had visited in the past month.

Everyone who stopped coming, which is the group whose dissatisfaction you most needed to measure, is absent from the sample by construction. That is survivorship bias: the units that failed are no longer in the population you can see.

Selection bias is the broader version. A political poll conducted through a smartphone app reaches people with smartphones and the app. A study of startup practices that samples currently operating startups excludes every one that shut down.

Non-response bias is the one that survives good sampling design. Draw a perfect random sample of 2,000 members, and if only 400 respond, you have a self-selected subsample of 400. People with strong opinions in either direction respond more, and the middle stays quiet.

Here is why more data does not help. Increase the survey from 400 to 40,000 responses collected the same way, and the standard error shrinks by a factor of ten while the bias stays exactly where it was. You end up with a tighter confidence interval around a wrong number, which is worse than a wide interval around it, because it invites confidence.

That distinction is what interviewers are testing: sampling error shrinks with n, bias does not.

What you can do. Compare respondents against the frame on variables you have for everyone: joining date, membership tier, visit frequency. If respondents visit twice as often as the full membership, you know the direction of the problem even if you cannot fix it. Follow up a random subsample of non-responders more aggressively, and compare them against the original responders. Weight by known population characteristics, accepting that weighting corrects only for the variables you measured.

And state the limitation in the report. An estimate labelled as covering active members only is useful; the same estimate presented as member satisfaction is misleading.

They get confused because both are measures of spread, but they describe entirely different things.

A logistics firm measures delivery times for 900 parcels. The mean is 38 hours, the standard deviation is 15 hours.

Standard deviation = 15 hours. Individual parcels vary a lot. Some arrive in 20 hours, some in 60. That number describes the parcels.

Standard error = 15 / sqrt(900) = 0.5 hours. If you repeated this exercise with a fresh sample of 900 parcels, the sample mean would land somewhere near 38 hours, typically within about an hour. That number describes how precisely you have pinned down the mean.

SE = s / sqrt(n)

Collect 90,000 parcels instead and the standard error drops to 0.05 hours, while the standard deviation stays at 15. More data makes you more certain about the average; it does not make deliveries more consistent.

The square root is the part with practical consequences. To halve the standard error you need four times the data. To get it down by a factor of ten you need a hundred times the data. That is why precision gets expensive quickly, and why a proposal to “just collect more data” needs a number attached.

Where the confusion causes real damage: an error bar labelled ambiguously. A chart showing mean delivery time with ±0.5 hour bars, read as if it described parcels, tells a manager that deliveries are extremely consistent. They are not; that bar describes the estimate, not the parcels. Label which one you plotted.

Choose by the question. Describing the customer experience needs the standard deviation, or better, percentiles. Stating how confident you are in the reported average needs the standard error.

Standard error is not exclusive to means. Any statistic has one, though the formula differs.

The correct statement is about the method, not about this interval.

Imagine drawing 100 independent samples and constructing an interval from each. About 95 of those intervals would contain the true population value. You have one of them, and you do not know whether it is one of the 95 or one of the 5. The parameter is a fixed number; the interval is what varies.

Three misreadings, each worth correcting explicitly.

“There’s a 95% probability the true value is between 3.1 and 4.7.” Under frequentist reasoning the parameter is not random, so it has no probability of being anywhere. It either is or is not in this interval. A Bayesian credible interval does support that phrasing, and it is a different object built on different assumptions. Naming that distinction is what separates a strong answer.

“95% of the data falls in this range.” No. That would be a prediction interval, and it is far wider. With a defect rate estimate of 3.9% ± 0.8%, individual batches vary far more than that.

“The values in the middle are more likely.” The interval carries no distribution of belief inside it. Values near the edge are not less plausible in any statement the interval makes.

The width itself is the useful information, and it is underused. An interval of 3.1% to 4.7% says the estimate is reasonably tight. An interval of 0.4% to 12.2% around the same point estimate of 3.9% says you know almost nothing, even though both report the same central figure.

On the zero question: an interval containing zero means you cannot rule out no effect at this sample size. It does not establish that the effect is zero. An interval running from −0.2% to +9.5% is entirely consistent with a large positive effect and is simply too imprecise to say.

Narrower comes from more data, less variability, or a lower confidence level, and the last one is buying width by accepting more misses.

For the packaging question, with spoilage rates:

H0: p_new = p_old      (no difference in spoilage rate)
H1: p_new < p_old      (new packaging reduces spoilage)

The null is the boring, sceptical position. It exists because you can only ever gather evidence against something, never conclusively for it. The logic is a proof by contradiction with probability attached: assume no difference, ask how surprising the observed data would be under that assumption, and reject only if the answer is “very”.

That asymmetry explains a question interviewers like. Why not make “the new packaging works” the null? Because failing to reject a null is not evidence for it. If your claim were the null and the test came back inconclusive, you would be treating “we could not disprove it” as support, which it is not. Putting the sceptical position in the null means the burden of proof sits with the claim.

Three things to get right.

State them before you see the data. Deciding on a one-tailed test in the direction the data happens to point doubles your effective false positive rate, and it is a well-known and easily detected form of cheating.

Choose one-tailed only when a change in the other direction would lead to the same decision as no change. If packaging that increased spoilage would matter, use two-tailed.

And a “fail to reject” outcome is not proof of equivalence. It means insufficient evidence at this sample size. If the business genuinely needs to establish that the two are the same, that requires an equivalence test with a stated margin, which is a different design.

Ask the interviewer what decision follows from the result. A test with no decision attached usually has the wrong hypothesis.

The definition has to be said carefully because the wrong version is more common than the right one.

A fertiliser trial reports p = 0.03 for a yield difference. What that means: if the fertiliser genuinely had no effect, you would see a difference this large or larger in about 3% of trials of this size, purely through sampling variation.

Four misreadings, and each has cost someone an offer.

“There’s a 3% chance the null is true.” That would require a prior probability of the null, which the p-value never uses. This is the same conditional-probability inversion as reading a positive test result as the probability of disease.

“There’s a 97% chance the effect is real.” Same error, restated. It also ignores that a real effect could be far smaller than the one you measured.

“p = 0.001 means a bigger effect than p = 0.04.” No. The p-value depends on effect size and sample size together. A trivial difference across two crore observations produces a tiny p-value. Report the effect size and its interval alongside.

“p = 0.049 is a finding and p = 0.051 is nothing.” The 0.05 threshold is a convention with no natural basis. Those two results are nearly identical evidence, and treating them as categorically different is what drives selective reporting.

Two structural points that matter more than the definition.

Multiple testing destroys the interpretation. Fourteen comparisons at the 5% level gives roughly a 51% chance of at least one result below 0.05 with nothing real going on. One hit out of fourteen is what chance produces, and reporting it as a finding without saying how many tests were run is the most common form of misleading analysis in industry.

And p = 0.06 does not mean the feature does not work. It means insufficient evidence at this sample size. Ask what the confidence interval looks like: if it runs from −1% to +14%, the honest answer is that the study was underpowered, not that the effect is absent.

Power is 1 − β, the probability of detecting a real effect when one exists.

For fraud detection, map the errors onto real consequences before answering.

A false positive blocks a legitimate transaction. The customer at a payment terminal is embarrassed, calls support, and possibly stops using the card. Cost: support handling, some churn, reputational damage.

A false negative lets a fraudulent transaction through. Cost: the transaction value, plus chargeback handling, plus regulatory exposure if it is systematic.

Put numbers on it. If a blocked legitimate transaction costs roughly ₹400 in support and churn, and a missed fraud averages ₹22,000, then one missed fraud costs as much as fifty-five false alarms. That ratio says tolerate false positives and tighten against misses.

Now flip the domain. For a screening test that triggers an invasive follow-up procedure, false positives carry real medical risk and the calculation runs the other way.

The point interviewers are testing is that neither error is universally worse. Anyone who answers “Type I is more serious” without asking about the application has recited a textbook.

The trade-off is real at fixed sample size. Lowering the threshold to catch more fraud necessarily flags more legitimate transactions; there is no threshold setting that reduces both. The only way to improve both simultaneously is a better model or more data, which is a different conversation from where to set the cut-off.

One thing worth naming: the base rate matters enormously here. When fraud is 0.1% of transactions, even a small false positive rate applied to the huge legitimate population produces far more false alarms than true catches, which is the same arithmetic that makes rare-disease screening produce mostly false positives.

Significance and importance are independent questions, and conflating them is one of the most common analytical failures in industry.

A bank tests a redesigned statement layout on 40 lakh account holders and finds that the digital payment rate rises from 62.0% to 62.3%. With that sample size, p = 0.002. The result is real.

Now do the business arithmetic. A 0.3 percentage point lift across 40 lakh accounts is 12,000 additional accounts using digital payments. If each is worth ₹90 a year in reduced processing cost, that is around ₹11 lakh annually. Set against a redesign, a testing cycle and a rollout costing ₹60 lakh, the answer is no.

The sample size is what made the p-value small, not the effect. Run the same test on 4,000 accounts and the same 0.3 point difference would be nowhere near significant. Nothing about the underlying effect changed; only your ability to detect it did.

Two things to bring into the room.

Report the effect size with its confidence interval, always, next to the p-value. An interval of 0.1% to 0.5% tells the business the plausible range of what they are buying. The p-value alone tells them only that it is not zero, which is rarely the question they asked.

And decide the threshold that matters before running the test. Ask the business what lift would justify the investment, and use that as the minimum effect of interest. A test designed around a 2% target that returns 0.3% has answered the question clearly, and the answer is no.

The reverse case deserves mention too. A large, commercially important effect measured on a small sample can come back non-significant, and dismissing it as “no effect” is equally wrong. The correct reading is that the study was too small to tell.

That example is famous, so use it to set up the general structure rather than dwelling on it.

An observed correlation between A and B has four possible explanations, and the data alone cannot distinguish them.

A causes B. The straightforward reading, and the one people jump to.

B causes A. Reverse causation, and it is easy to miss. A hospital finds that patients receiving a certain intensive treatment have higher mortality. The treatment is given to the sickest patients; severity causes both the treatment and the outcome.

A third variable causes both. The ice cream case. In business data this is everywhere: a company observes that customers who use its mobile app spend more. Engaged, higher-income customers both download apps and spend more. The app may add nothing.

Chance. With enough variables compared, some pairs correlate strongly for no reason at all. Compare 200 metrics pairwise and you have 19,900 correlations; a few will look impressive.

The confounder problem is what makes this hard rather than merely a caution. You can control for the confounders you thought of and measured. You cannot control for the ones you did not, and there is no statistical test that tells you an unmeasured confounder exists. That is a genuine limitation of observational data, not a technique problem.

What establishes causation: randomised assignment, because randomising breaks the link between the treatment and every confounder, measured or not. Where randomisation is impossible, quasi-experimental designs such as difference-in-differences, instrumental variables or regression discontinuity make explicit assumptions that let you argue for causation, and those assumptions are the weak point to interrogate.

The answer interviewers want is not “correlation isn’t causation” recited back. It is the question that follows: what would have to be true for the causal reading to hold, and can you check it?

A distributor is deciding whether to extend ₹8 lakh of credit to a new retailer.

If the retailer pays, the distributor earns ₹1.2 lakh in margin. If the retailer defaults, ₹8 lakh is lost. Based on the credit assessment, the default probability is 8%.

EV = 0.92 × 1,20,000  +  0.08 × (−8,00,000)
   = 1,10,400 − 64,000
   = ₹46,400

Positive, so on average this decision makes money. Across a hundred such retailers, the distributor comes out roughly ₹46 lakh ahead even though eight of them will not pay.

The break-even is worth computing too, because it is more useful than the point estimate. Set the expression to zero and solve for the default probability: it flips negative once the default rate rises above about 13%. Now you can ask whether 8% is plausibly off by five points, which is a far more answerable question than whether it is exactly right.

Three limits to state in an interview.

Expected value is a long-run average and there is no long run for a one-off decision. Extending ₹8 lakh once, to a business whose entire cash reserve is ₹8 lakh, is a bet with positive expected value that can end the business. This is why insurance exists and is rational despite having negative expected value for the buyer.

The number inherits every assumption in the probabilities. If the 8% came from a model trained on a different retailer segment, the EV is arithmetic performed on a guess.

And outcomes are rarely two-valued. Partial recovery through settlement, delayed payment with interest cost, and the value of a retailer who becomes a long-term customer all belong in a realistic version.

Ask the interviewer whether this decision repeats. If it does, follow the expected value. If it does not, and the downside is unrecoverable, say so.

The distinguishing question: is there a fixed denominator?

Binomial. A telecom operator sends 500 service SMS messages; each has a 3% chance of failing to deliver. Fixed n = 500, fixed p = 0.03, and you are counting how many of those 500 fail. Expected failures = 500 × 0.03 = 15. Variance = np(1−p) = 14.55.

Poisson. A helpdesk receives calls at an average of 12 per hour. There is no “number of trials” here; calls arrive continuously and there is no upper bound on how many could arrive in an hour. Expected = 12, and the defining property is that the variance also equals 12.

That equality is the Poisson’s signature and its main diagnostic. If observed call counts have a mean of 12 and a variance of 40, the Poisson assumption is wrong. Usually that means the arrival rate is not constant, calls cluster after an outage, or the intervals are not comparable.

The two connect. When n is large and p is small, binomial converges to Poisson with lambda = np. With n = 10,000 and p = 0.0002, computing binomial probabilities involves enormous factorials, while Poisson with lambda = 2 gives essentially the same answers and is far easier to work with.

Both assume independence, and that is where real data most often breaks them.

For the SMS case, if failures are caused by one network element going down, the messages routed through it fail together. The mean is still 15, and the variance is far larger than 14.55, so any interval or test built on binomial assumptions is too narrow. Manufacturing defects behave the same way when a bad raw material batch causes correlated failures.

The practical check is to compare the observed variance against what the model predicts. Overdispersion is common enough that negative binomial is often the honest alternative to Poisson.

They answer different questions and get merged constantly.

A quality inspector samples finished ceramic tiles. The true defect rate is 4%.

Law of large numbers. Inspect 50 tiles and you might see 1 defect, or 5, so an observed rate of 2% or 10%. Inspect 50,000 and the observed rate will sit very close to 4%. The sample mean converges to the population mean as n grows. That is a statement about where the estimate goes.

Central limit theorem. At n = 1,000, how far off might you be? The standard error of the proportion is:

SE = sqrt(0.04 × 0.96 / 1000) = 0.0062

So roughly 95% of samples of 1,000 give an observed rate between about 2.8% and 5.2%. That is a statement about the spread around the true value at a given n, and it is what makes confidence intervals possible.

The misconception both are used to justify is the gambler’s fallacy. If this month produced far more defects than expected, nothing “corrects” it. Future output is unaffected by past output, assuming the process has not changed. What happens is dilution: the excess becomes a smaller fraction of a growing total, so the running average drifts back toward 4% without any compensating run of good tiles.

Say that clearly, because the phrase “it evens out” describes the wrong mechanism and interviewers listen for it.

Neither theorem guarantees anything about one particular sample. Both describe behaviour as n grows or across repeated samples.

Right skew is the normal condition for business quantities, not an anomaly. Time on a page, order values, city populations, page views per article, and firm revenues are all bounded below by zero with no upper bound, so the tail can only run one way.

Take article page views on a news site over a month:

median: 1,400
mean:   9,800
max:    2,40,000

The mean is seven times the median because a handful of viral pieces dominate. Any technique that treats the mean as typical will mislead.

Logs help in two specific situations.

When the underlying relationship is multiplicative. If a headline change increases views by 30% rather than by 400 views, that is multiplicative, and taking logs turns it into an additive effect that linear methods can handle. The coefficient then reads as an approximate percentage change, which is often what the business wanted anyway.

When a method assumes roughly symmetric errors. Fitting on raw views lets three viral articles dominate the fit entirely.

Three things logs do not fix.

Zeros. log(0) is undefined. Adding a small constant is common and it is a genuine choice, not a neutral one, since the result depends heavily on the constant you pick. For count data with real zeros, a model built for counts is usually more honest than a shifted log.

Negative values. Logs are simply unavailable, so profit or temperature change need a different approach.

Interpretation. Exponentiating a prediction from a log-scale model gives approximately the geometric mean, not the arithmetic mean, and those differ substantially on skewed data. If someone needs a revenue forecast to add up, that gap matters.

If the goal is description rather than modelling, you often do not need a transform at all. Report the median, the quartiles and a few high percentiles, and show the histogram on a log-scaled axis so the shape is visible without altering the numbers.

Uniform shows up less often in nature than people expect. Where it genuinely applies: random number generation, allocation of applications to reviewers by a randomising system, and rounding error, where a value rounded to the nearest rupee has an error uniformly spread between −0.5 and +0.5.

For a continuous uniform between a and b, the mean is (a+b)/2 and every subinterval of equal width has equal probability. That last property is what makes it a poor model for most measured quantities, which cluster around a typical value rather than spreading flat.

Exponential describes the gap between events when events arrive at a constant average rate.

A power distribution feeder experiences faults at an average of 2 per month. The time until the next fault is exponential with mean 1/2 = 0.5 months. The probability of going more than a month without a fault is:

P(T > 1) = e^(-2 × 1) = e^(-2) = 0.135

About a 13.5% chance of a clear month.

The memoryless property is the part interviewers probe. If the feeder has already run 20 days without a fault, the distribution of remaining time is exactly the same as it was on day one. No fault is “due”. That is a genuine property of a constant-rate process and it is exactly why exponential is the wrong model for equipment wear, where failure probability rises with age. Weibull handles that case.

The link worth stating: if events per interval are Poisson with rate lambda, the gaps between events are exponential with mean 1/lambda. They are two views of the same process.

For a bus wait, neither is automatically right. If buses run to a schedule you do not know, arriving at a random time gives a roughly uniform wait within the headway. If they arrive erratically at a constant average rate, exponential fits better. Ask which situation you are in.