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In Type Ia supernova cosmology, the predicted apparent magnitude depends on the common absolute magnitude $M_0$ and the Hubble constant only through $\beta =M_0-5{\log }_{10}(H_0/H_{\mathrm{ref}})$, after choosing a fixed reference $H_{\mathrm{ref}}>0$. A flat improper prior on $M_0$ makes the likelihood integrated over $M_0$ independent of $H_0$, by translation of the integration variable. If the other prior factors are independent and the posterior is proper, the marginal posterior of $H_0$ equals its prior. An external calibration of $M_0$ can break this lack of identifiability.

Additional measurements and anatomical identifiability asks which observations distinguish the anatomical quantities that a measurement model aims to recover. More observations help only if they constrain information missing from the existing measurements. Repeating one height measurement and measuring an independent dimension are different operations.

Formally, let $F(\theta )$ denote the observations predicted from shape parameters $\theta$, and let $S(\theta )$ be the desired surface area. The area is identifiable from those observations precisely whenthroughout the allowed model class. This is quantity-specific identifiability: identifying a target need not require reconstructing every shape parameter. Measurement precision is a separate issue from this structural property.

Extend the original cuboid construction in non-identifiability of shape from height and mass. Fixed height $H$, mass $M$ and assumed uniform density $\rho$ determine $A=ab=M/(\rho H)$, but not the side lengths $a,b$. An additional horizontal perimeter measurement $P=2(a+b)$ determines the total surface area:For stipulated $H=1.5\mathrm{m}$, $M=60\mathrm{kg}$, $\rho =1000kg/{\mathrm{m}}^3$ and $P=1.0\mathrm{m}$, this gives $A=0.040{\mathrm{m}}^2$ and $S=1.58{\mathrm{m}}^2$. The horizontal sides solve the quadratic equation $z^2-(P/2)z+A=0$, giving $0.40$ and $0.10\mathrm{m}$. Their interchange leaves the same area. A square section of the same $A$ has $P=0.80\mathrm{m}$ and total area $1.28{\mathrm{m}}^2$; height and mass alone could not distinguish these cases.

The conclusion relies on the stated geometry and density. A circumference at one location does not generally determine the entire body surface area of an arbitrary person. Two shapes can share that circumference and differ elsewhere. Validation therefore needs independent geometric evidence and a justified model class, not simply a larger number of inputs. The GUM likewise requires relevant model quantities and corrections to be included rather than equating precise inputs with complete knowledge.^[ref]

Local sensitivity also deserves attention. In the parameterization $a=\sqrt{A}{e}^t$, $b=\sqrt{A}{e}^{-t}$, the perimeter is $P(t)=4\sqrt{A}\cosh t$. Its derivative vanishes at the square $t=0$, and $P(t)-P(0)=2\sqrt{A}{t}^2+O(t^4)$. Small departures from a square can therefore be difficult to resolve from a noisy perimeter even when exact observations determine the area. Structural identifiability and practical precision answer different questions.

Bearing thermal stiffness identification uses measured force changes along a specified thermal path, together with independently known expansion behavior, to infer the axial restraint of an assembly. The observed bearing thermal reaction slope is $q=dF/dT$ inN/K. Mechanical stiffness is force per displacement, so converting $q$ into stiffness requires the free relative-expansion rate $\beta$ in displacement per temperature. In the constant-compliance engaged model,Here $C_b$ and $C_s$ represent the bearing and supporting structure's axial mechanical compliance contributions.

For an original identification example, suppose equilibrated engaged measurements give forces160,320 and480N at temperature increases50,60 and70K. A linear regression gives slope16N/K and, within this model, an extrapolated zero-force engagement increase of40K. If an independent free-expansion measurement gives $\beta =2\mu m/K$, the total compliance is $0.125\mu m/N$ and total stiffness is $8N/\mu \mathrm{m}=8\times 10^{6}N/m$. A16N/K thermal slope is therefore not itself a16N/m spring stiffness.

The measurements have an identifiability limit: the slope determines $C_b+C_s$ when $\beta$ is known, rather than determining both contributions separately. A known supporting-structure compliance $C_s=0.100\mu m/N$ would imply $C_b=0.025\mu m/N$. Without that extra information, many pairs give the same total. If $\beta$ is also unknown, scaling both $\beta$ and total compliance by the same positive factor leaves the measured slope unchanged.

A bench experiment can measure axial force with a load cell, track shaft and housing temperatures, wait for equilibrated states and fit only measurements from the engaged regime. A separate low-restraint expansion measurement can estimate $\beta$. Repeating heating and cooling helps test whether friction, changing contact or thermal gradients invalidate the assumed single slope. These are proposed measurement steps, not a claimed manufacturer's experiment. The physical motivation is the need to accommodate relative thermal displacement in a locating/non-locating bearing arrangement.^[ref]

For independent $\beta$ and $q$, first-order propagation givesFor $\beta =2.0$ with standard uncertainty0.1µm/K and $q=16.0$ with standard uncertainty0.8N/K, the inferred total compliance has standard uncertainty about0.00884µm/N. Correlated temperature references require the corresponding covariance contribution rather than this independent-input expression.^[ref]

The Bradley-Terry model assigns positive abilities ${\theta }_i$ and the displayed pairwise winning probabilities. Multiplying all abilities by the same positive scalar leaves the probabilities unchanged, so identifiability requires a normalization. In log abilities ${\beta }_i=\log {\theta }_i$, the model has comparison probabilities obtained from the logistic function. Either parametrization induces the same ordering of players.

A capture-recapture model is a statistical model for repeated observations of identifiable individuals, including those missed on some occasions. A closed-population capture-recapture model estimates a fixed population cardinality; models allowing individuals to enter or leave can instead describe survival and recruitment. The sampling assumptions determine which likelihood function is appropriate.

For the two-sample closed-population capture-recapture model, condition on the sample sizes $M$ and $C$. If the second sample selects $C$ distinct individuals from $N$ by simple random sampling, then the overlap $R$ has the hypergeometric distribution:Here $r$ is an integer and the probability mass function is zero outside these bounds. The binomial coefficients count choices of $r$ marked and $C-r$ unmarked individuals, divided by all equally likely size-$C$ subsets. The hypergeometric distribution has expected valueEquating the observed overlap with this expected value gives the Lincoln-Petersen estimator. The underlying sampling without replacement, probability mass function, and expected value are developed in Raymond P. Guiteras, MIT 14.30 hypergeometric distribution handout, §§1–4 and 8.

For the toy counts $M=20$, $C=25$, and $R=5$, hold the observations fixed and vary the unknown integer $N$. The likelihood function isValues below forty cannot contain the observed set union. Exact comparison of consecutive likelihoods gives two tied maximum-likelihood estimates, $N=99$ and $N=100$. The Lincoln-Petersen estimator returns $100$; the Chapman estimator returns $90$ and is a different rule for estimation.

The vertical scale is $L(N)/{\max }_{n\ge 40}L(n)$. This relative likelihood compares how well candidate statistical parameters explain the same observations; it is not a posterior probability. The displayed range $40\le N\le 300$ is only a plotting window. The likelihood function remains positive for every integer $N\ge 40$ and tends to zero as $N$ increases, so the curve has a continuing right tail. The data do not justify truncating statistical inference at three hundred. The conditional hypergeometric distribution formulation also appears in Louis-Paul Rivest and Mamadou Yauck, Small Sample Estimators for Two-way Capture Recapture Experiments, §3, equation (5).

Zero recaptures require care. With $R=0$ and positive $M,C$, the Lincoln-Petersen estimator has no finite ratio, but the capture-recapture model still gives a valid likelihood function:This likelihood function increases toward one as $N$ grows, so there is no finite maximum-likelihood estimate. For the same sample sizes twenty and twenty-five with zero overlap, forty-five distinct individuals would be observed. Lack of overlap supplies a lower bound but very weak information about large population cardinalities.

In more elaborate capture-recapture models, a first-recapture array $m_{ij}$ counts individuals released at occasion $i$ and next observed at $j$. A probability of survival ${\varphi }_j$ and a probability of detection $P_{j+1}$ contribute a no-observation continuation factor ${\varphi }_j(1-P_{j+1})$. The resulting likelihood function depends on both survival and detection; these probabilities need not be separately identifiable at the last observation interval. Missing-count EM for capture-recapture describes one way to fit such a model, and identifiability remains a separate issue from computing an estimator output.

An original toy model separates two ways to lose a central cathode ray signal. Let $x$ be forward depth into a uniform gas. Normalize the entering electron population to one. Write $U(x)$ for the fraction still in a narrow forward channel, and $D(x)$ for the fraction diverted into a wider collection channel. Assume constant removal rate $a$ per unit depth in both channels, and constant transfer rate $b$ from $U$ to $D$, with no return. Removal means that an electron stops or is trapped before reaching the collecting plane; it does not mean that its electric charge disappears. The wide ideal collector accepts all surviving members of both channels. This is a stipulated two-population differential equation model, not a general law of electron transport:The first equation gives exponential decay. Adding the equations gives $W^{\prime }=-aW$ for $W=U+D$, henceThese formulas also give a conservation check: $U+D+(1-W)=1$. The fraction $1-W$ has been removed before the plane, while $D$ remains present but misses the narrow collector. An exponential fit to the narrow signal therefore measures $a+b$, not the removal rate $a$ by itself. This is an identifiability issue: one declining signal cannot distinguish the two unknown rates.

For a worked example, choose $a=0.15\mathrm{c}{\mathrm{m}}^{-1}$ and $b=0.35\mathrm{c}{\mathrm{m}}^{-1}$. These are invented teaching inputs, not measured coefficients for air or Lenard's apparatus. At $x=2.00\mathrm{cm}$,Thus about $63.2\%$ misses the narrow collector, although only about $25.9\%$ has been removed in this model. Treating the whole narrow-signal deficit as stopping would confuse redistribution with removal.

Suppose a calibrated readout is proportional to arriving electron number with the same response for either channel. Choose an empty-path signal $R_0=1020$ arbitrary units, of which $B=20$ is background; the two collection geometries have the same calibrated reference. The calculated readings at $2\mathrm{cm}$ are $R_{\mathrm{n}}=20+1000e^{-1}\simeq 387.88$ and $R_{\mathrm{w}}=20+1000e^{-0.3}\simeq 760.82$. After background subtraction, define $T_j=(R_j-B)/(R_0-B)$ for each geometry. Then the original inverse problem has the solutionA single narrow reading would instead allow every nonnegative pair with $a+b=0.50\mathrm{c}{\mathrm{m}}^{-1}$. Using the raw ratios without subtracting $B$ gives an erroneous narrow rate of about $0.4834\mathrm{c}{\mathrm{m}}^{-1}$. In a real fluorescent screen, the assumed response must be tested: deposited energy and conversion to light need not remain constant as electrons slow. Repeating the comparison at several depths tests the constant slopes, although straight slopes alone do not establish the microscopic mechanism.

Actual electrons change kinetic energy and direction. Electron stopping power $S(K)=-dK/ds>0$ describes mean kinetic energy loss per travelled path length $s$; collisional losses include ionization, while radiative losses include bremsstrahlung. The continuous slowing-down approximation range integrates reciprocal total electron stopping power, neglecting fluctuations. It approximates travelled path length, not forward penetration depth.^[ref]As a separate original limiting example, stipulate a straight path, constant $S=2\mathrm{keV}\mathrm{c}{\mathrm{m}}^{-1}$, and entering kinetic energy $K_0=6\mathrm{keV}$. Then $K(s)=6\mathrm{keV}-Ss$ until stopping, and $R_{\mathrm{CSDA}}=3\mathrm{cm}$. In that deterministic model every entering electron reaches each depth below $3\mathrm{cm}$ and none crosses a plane beyond it. There is no exponential population tail. Real fluctuations and electron scattering make the situation more complicated, but the example already proves that continuous energy loss does not imply constant-rate removal.

The window also changes the entering population: source kinetic energy before the foil need not equal $K_0$ just outside it. For an electron initially at rest, an ideal static accelerating electric potential difference $V>0$ supplies electrical work $eV$, where $e$ is the elementary charge. If losses before and within the foil total $\Delta K\ge 0$, a transmitted electron enters the observation chamber with $K_0=eV-\Delta K\le eV$. A screen's brightness determines neither $V$ nor $\Delta K$. These formulas specify a modern ideal work-energy theorem argument; no numerical historical voltage or foil thickness is inferred from the diagram.

An integer pattern must survive the stated measurement uncertainty. For an original simulated example, choose a reference electric charge $Q_{\ast }>0$, define $y_i=|q_i|/Q_{\ast }$, and stipulate state meansHere each ${\sigma }_i$ is an independent standard uncertainty of a state mean, before shared calibration effects. The generator constructs repeated noisy observations with these means; the numbers are deliberately chosen, not historical data. There is no conversion of $Q_{\ast }$ to coulombs and no measured value of the elementary charge in this example.

For a candidate spacing $a>0$ in units of $Q_{\ast }$ and proposed integers $n_i$, use weighted least squares:The last two expressions follow by differentiating the quadratic in $a$ and propagating the independent errors. They are conditional on fixed, correct integer assignments and the stated error model. They do not include uncertainty from choosing those assignments. For $\mathbf{n}=(2,3,5,4)$, they give $\hat{a}=1$, $u(\hat{a})\simeq 0.01089$, and ${\chi }^2=0.46875$. Such a small residual is compatible with this chosen error scale; it is not evidence that the errors vanish. A chi-squared distribution interpretation additionally needs the appropriate normal distribution error model and allowance for the fitted parameter; searching many assignments changes that interpretation.

The obstruction is identifiability: replacing $(a,n_i)$ by $(a/m,m{n}_i)$ for any positive integer $m$ leaves every predicted reading unchanged. In particular, an $e$-spaced pattern also fits an $e/2$ lattice using even indices. Even the coarsest well-fitting spacing need not be the physical unit: a dataset containing only even charge states can have twice that unit. Worse, if arbitrarily fine spacings and unrestricted integers are allowed, rounding each $y_i/a$ givesConsequently a finite fit cannot prove a minimal transferable electric charge. Reproducible smallest observed jumps supply additional evidence; interpreting them as single-carrier transfers requires independent physical support. One visibly abrupt transition could contain several unresolved transfers. In the simulation the successive differences are $0.93$, $2.06$, and $-1.03$, each with standard uncertainty $\sqrt{2}(0.08)\simeq 0.1131$. These support changes near $a,2a,-a$ conditional on that unit; they equally support $2,4,-2$ units of $a/2$. Neighboring differences share a state reading and are therefore correlated, even though the state means were stipulated independent.

A shared scale error can preserve every apparent integer relation. To first order, an independent fractional scale standard uncertainty $s$ adds $s^2{a}^2{n}_i{n}_j$ to the covariance matrix of the $y_i$. For the simulation, stipulating $s=0.02$ changes the conditional uncertainty of $\hat{a}$ to approximately $\sqrt{0.01089^2+0.02^2}=0.02277$, despite the same residual pattern. Repeating timings cannot average away this common scale contribution. In the uncorrected continuum model in elementary charge, holding the other measured inputs fixed gives $|q|\propto {\eta }^{3/2}$, so a small fractional error in air dynamic viscosity causes $3/2$ times that fractional error in inferred electric charge. The gas slip correction to Stokes drag requires its own propagation. Pattern agreement, drop-stability controls and absolute measurement calibration together make the inference persuasive within resolution.

On a compact parameter space, suppose the expected log-likelihood is continuous, uniquely maximized at the true parameter, and the normalized empirical log-likelihood converges uniformly in probability to its expectation. On the compact complement of every neighbourhood of the truth, the expected criterion has a strictly positive gap below its maximum. Uniform approximation by less than one-third of this gap excludes every empirical maximizer from that complement. Identifiability and nonnegativity of Kullback-Leibler divergence supply the unique expected maximizer. The proof works for any measurable choice of maximizer.

If the conditional error distribution function is continuous and strictly increasing with $\tau$-quantile zero, the conditional expected check loss is uniquely minimized at zero fitted displacement. If every incorrect parameter differs from the true regression function on an event of positive probability, averaging these nonnegative conditional risk differences gives strict identifiability of the true parameter. Integrable errors and bounded regression functions supply finite risks.

If each level of one categorical variable belongs to exactly one level of another, indicators for the coarser levels are sums of indicators for the finer levels. Including unrestricted fixed effects for both therefore gives a rank-deficient ordinary least squares: the separate effects lack identifiability without additional constraints.

One observed radiative flux cannot determine both luminosity and Euclidean distance: for every $k>0$, replacing $(L,d)$ by $(k^{2}L,kd)$ leaves $F$ unchanged. In particular, $4\times 10^{26}\mathrm{W}$ at $40$ parsecs produces the same observed radiative flux as $10^{26}\mathrm{W}$ at $20$ parsecs. This is a concrete failure of identifiability in an inverse problem.

An independent stellar parallax fixes the distance and breaks this degeneracy; alternatively, a calibrated standard candle supplies the luminosity. Interstellar extinction can further reduce the observed radiative flux, and a photometric passband measures only a selected spectral range. At cosmological distances, use luminosity distance in the bolometric relation. Each inference must specify which radiative flux was measured and what propagation assumptions connect it to luminosity.

Formazan recovery identifiability asks whether measurements distinguish the amount of formazan formed from the fraction recovered in the optical reading. Better repeatability does not necessarily separate those quantities.

Let $n$ be total product formed, $r\in [0,1]$ the dissolved formazan recovery fraction, and $K=ϵ\ell /V$ a known optical conversion factor in a suitable fixed-path solution model. Then net absorbance isThe manufacturer's procedure separates formation of crystals, dissolution and measurement, motivating these distinct model quantities.^[ref] Knowing $B$ and $K$ determines the dissolved amount $d=B/K=rn$, but not the two parameters separately.

For any admissible scale $a>0$, replacing $(r,n)$ by $(ar,n/a)$ leaves $d$ unchanged, provided $ar\le 1$. For observed $d=6\mu \mathrm{mol}$, both $(r,n)=(1,6\mu \mathrm{mol})$ and $(1/2,12\mu \mathrm{mol})$ fit. In this conserved-product model the bound $r\le 1$ implies $n\ge d$, with no finite upper bound supplied by that measurement alone. This is an identifiability limitation, rather than merely a large measurement uncertainty.

Changing volumes or optical paths can provide several known factors $K_j$, but measurements $B_j=K_{j}rn$ still determine only the same product if $r$ and $n$ stay fixed. Such changes can test the optical law without resolving the underlying ambiguity.

An original matched-addition model illustrates what extra information could help. Suppose a known amount $\Delta n$ is added before the recovery step and experiences exactly the same unknown fraction $r$ as the native product. Converting both readings to dissolved amounts givesIf $d_0=6\mu \mathrm{mol}$ and adding $2\mu \mathrm{mol}$ increases the dissolved amount by $1\mu \mathrm{mol}$, the model gives $r=0.5$ and $n=12\mu \mathrm{mol}$. Adding already dissolved product after the recovery step would instead test later optical response and would not identify earlier losses.

The shared-recovery assumption must be justified: a dissolved spike can behave differently from product crystals formed inside a preparation. A second measurement helps only if its relation to the unknown quantities is independently established. Repeated measurement of the same product $rn$ cannot supply that missing relation.

Fit the positions of successive, consistently defined troughs by linear regression, $V_n=b+nd+{ϵ}_n$. A constant intercept $b$ absorbs the contact potential difference, collection phase and initial energy effects; $d$ estimates the repeated loss expressed as a voltage. Subtracting successive positions cancels $b$. A line fit uses every position and leaves residuals that can reveal curvature or a misidentified trough. It still assumes that the phase is constant over the fitted range and that all troughs belong to the same loss channel.

For an original numerical example, choose $n=1,2,3,4,5$ and synthetic positions $V_n=(6.62,11.46,16.48,21.30,26.14)\mathrm{V}$. Their successive spacings are $(4.84,5.02,4.82,4.84)\mathrm{V}$. The ordinary least squares formulas giveThe fitted residuals are $(-0.004,-0.052,0.080,0.012,-0.036)\mathrm{V}$, with zero sum and zero index-weighted sum. Their residual sum of squares is $0.01056{\mathrm{V}}^2$. If independent, equal-variance, zero-mean errors describe these positions, the residual variance estimate is $s^2=0.01056/(5-2)=0.00352{\mathrm{V}}^2$ and the slope standard error is $s/\sqrt{10}=0.01876\mathrm{V}$. Thus the inferred model loss is $4.888\mathrm{eV}$ with conditional standard error $0.01876\mathrm{eV}$. These errors summarize only the chosen position scatter; a voltage-scale error or a drifting collection phase is not included. Adjacent spacings share a position error and are therefore correlated even when position errors are independent.

The offset has a sharper identifiability limitation. Even if a constant-phase model were exact, an initial beam kinetic energy $E_0$ shifts the troughs by $-E_0/e$. For the symmetric illustrative curve, $b=V_c-E_0/e+V_r/2$. The transformation $V_c\mapsto V_c+\alpha$, $E_0\mapsto E_0+e\alpha$ leaves every trough position unchanged. Measuring $b$ alone therefore cannot determine the contact potential difference. Relabeling $n\mapsto n+m$ also changes $b$ by $-md$ without changing $d$. An independent offset calibration and a justified collection model are needed before turning a first trough into an excitation threshold. Varying $V_r$ tests this model's predicted half-voltage shift of the trough centers; it is a diagnostic prediction of this chosen curve, not a universal correction for experimental minima.

High-dimensional statistics studies inference when the number of variables or parameters is large relative to the number of observations, often allowing both to grow. The difficulty is structural rather than merely computational: with an $n\times p$ design matrix and $p>n$, the null space is nontrivial, so $X\beta =X(\beta +v)$ for every $v$ in that null space.

The data alone then cannot identify an arbitrary coefficient vector. Assuming a sparse vector of regression coefficients can make restricted recovery possible when the design matrix is injective on the allowed differences. Regularization encodes or exploits such structural assumptions. A fitted model with many parameters is therefore not automatically informative about every parameter; identifiability and uncertainty depend on the model's structure and sampling design.

Homogeneity-study time-term identifiability asks whether a measurement schedule supplies enough independent information to distinguish instrumental drift from differences between containers. Adding time to a regression analysis does not guarantee that its coefficient can be estimated separately from the container effects.

In an original fixed-container measurement model,each container has an unknown intercept $a_i$ and all share a linear drift rate $\gamma$. If every observation of container $i$ occurs at one time $t_i$, any rate ${\gamma }^{\prime }$ gives the same predictions after replacing $a_i$ by $a_i+(\gamma -{\gamma }^{\prime })t_i$. The data cannot distinguish those parameter sets. Algebraically, the time column lies in the span of the container-indicator columns of the design matrix.

Repeated observations at different times within at least one container can break that exact ambiguity. Subtract each container's mean:For independent, equal-variance errors with variance ${\sigma }^2$, the least-squares drift estimate hasprovided the denominator is positive. The formula distinguishes identifiability from precision: a positive but tiny within-container time spread permits a formally unique yet noisy estimate.

For three containers each observed twice one time unit apart, the denominator is $3/2$. If each pair is instead separated by five time units, it is $75/2$. With the same residual variance and a valid linear-drift model, the latter schedule reduces drift-estimate variance by 25, or its standard deviation by five. These are design calculations, not a guarantee that a longer experiment remains linear or stable.

Randomized order and controls address additional risks. The primary IUPAC protocol requires randomized analysis of duplicate portions and inspection for suspect data features.^[ref] NIST's comparison designs also use observation order to suppress specified drift contributions.^[ref]

Record timestamps and check the rank of a matrix for the fitted design, but also assess residual time patterns, uncertainty and physical plausibility. A randomized schedule can still have poor numerical leverage; a full-rank model can still be wrong. Drift-aware homogeneity analysis must report those distinctions rather than equating a returned regression coefficient with established material homogeneity.

Maximum likelihood estimation is a method of statistical estimation: within a specified statistical model, choose the statistical parameter values that maximize the likelihood function of the observed data. For a parameter set $\Theta$ and observations $x$, its exact requirement isThe equality requires an attained, finite maximum; a supremum approached only at an excluded boundary is not enough. The resulting rule is a maximum-likelihood estimator. The likelihood function uses a probability mass function for discrete data and a probability density function for continuous data. See MIT 18.05, Reading 10b, sections 3 and 3.2.

The direction of the comparison is the interesting part: hold the observations fixed and vary the statistical parameter. Ten independent Bernoulli trials with eight successes and two failures give the maximum-likelihood estimate $\hat{p}=0.8$, as derived in log-likelihood. This chooses the member of the statistical model that assigns the greatest mass to that outcome. It does not assert an $80\%$ posterior probability that this parameter value is true. Bayesian statistics combines the same likelihood function with a prior distribution to obtain a posterior distribution; maximum a posteriori estimation maximizes that posterior mass or density instead.

The method turns many fitting tasks into one maximization problem. In the normal distribution model with known variance, it recovers the sample mean and ordinary least squares, while binomial regression and Poisson regression use different sampling assumptions to build their own likelihood functions. The log-likelihood turns independent contributions into a sum, exposing score equations and observed information. A peak's location gives an estimate; its shape records how much the observed data distinguish nearby parameter values.

Existence, uniqueness, bias, and statistical consistency are separate questions. Normal mean and variance maximum-likelihood estimators include a variance estimate with bias, likelihood supremum at an excluded boundary gives nonexistence, and the Neyman-Scott incidental parameter problem gives inconsistency. The usual asymptotic normality of a maximum likelihood estimator requires assumptions: a consistent estimator at an interior true parameter in a fixed finite-dimensional model with identifiability, sufficient smoothness and control of log-likelihood derivatives, and finite nonsingular Fisher information. A common parameter-independent support of a probability distribution is part of a standard sufficient framework; see Rigollet, MIT 18.650, Maximum Likelihood Estimation, slides 22-23. This is a description of the regular setting, not a complete theorem's hypotheses. The exact endpoint limit for a shifted exponential distribution shows why changing support can produce a different rate and a nonnormal limit. These properties do not follow just from maximizing a function.

In his 1922 paper in the Royal Society's Philosophical Transactions A, R. A. Fisher explicitly distinguished likelihood from probability and described choosing the parameter values with greatest likelihood. Section 6 also discusses comparing likelihoods after giving the maximum value one, the convention used in the figures here. See Fisher, On the Mathematical Foundations of Theoretical Statistics, section 6, pp. 326-328, DOI 10.1098/rsta.1922.0009.

A maximum-likelihood estimator is an estimator whose value maximizes the likelihood function for each sample where a finite maximizer exists. Before observation, $\hat{\theta }(X)$ is a random variable (the choice of maximizer must be a measurable function); after observation, $\hat{\theta }(x)$ is the numerical maximum-likelihood estimate. A formula must specify the allowed parameter set, including whether its endpoints belong to it.

For ten independent Bernoulli trials, write $K={\sum }_{i=1}^{10}{X}_i$. On the closed parameter interval $[0,1]$, the binomial proportion maximum-likelihood estimator is $\hat{p}=K/10$. Eight successes give the estimate $0.8$. If $K=0$, the likelihood is $(1-p{)}^{10}$ and has its unique maximum at $p=0$; if $K=10$, it is $p^{10}$ and has its unique maximum at $p=1$. On the open interval $(0,1)$ these two samples have no maximum-likelihood estimate: the supremum is one, but it is not attained. This is the same issue as likelihood supremum at an excluded boundary.

A complete continuous example uses independent and identically distributed random variables $X_i\sim N(\mu ,1)$ with unknown mean $\mu \in \mathbb{R}$ and known standard deviation one. Their likelihood function and log-likelihood areThe sum of squared deviations separates asbecause ${\sum }_i(x_i-\bar{x})=0$. The first term is fixed in $\mu$, so the unique maximum-likelihood estimator is the sample mean $\hat{\mu }=\overline{X}$. This also proves the equivalence with ordinary least squares for this model. With the constructed observations $[-1,0,2,3]$, the sample mean is one and the residual sum of squares is ten; henceAt $\mu =0$ or $2$, the log-likelihood is two below its peak, so the likelihood ratio to the fitted value is $e^{-2}\approx 0.135335$. The absolute likelihood at the peak is $(2\pi {)}^{-2}{e}^{-5}\approx 0.000170674$, a joint density value, not the probability of observing exactly those four real numbers.

The following figure compares that sample with a constructed sixteen-observation sample consisting of four repetitions of the displayed four values, modeled as sixteen independent draws. Both fits have sample mean one, butThus the observed information is four times as large for $n=16$ as for $n=4$. The distance from the peak at relative height $e^{-2}$ decreases from one to $1/2$: the width scales as $1/\sqrt{n}$. This is a comparison of two stipulated samples; merely copying recorded observations would not create new independent evidence.

Even uniqueness needs checking. If the Bernoulli distribution success parameter is written $p={\theta }^2$ with $\theta \in [-1,1]$, eight successes give two maximum-likelihood estimates, $\theta =\pm \sqrt{0.8}$, because both give the same probability distribution. The problem is a failure of identifiability. The special cases below show other ways an MLE can have bias or fail the usual asymptotic normality.

Simultaneously applying a permutation to the mixture weights and mixture components leaves $f$ unchanged. Thus identifiability of named components requires a convention, such as ordering distinct component means; label switching describes the associated inferential issue.^[ref]

Even after choosing label names, identical mixture components reveal only their combined mixture weight, and an inactive mixture component has undetermined statistical parameters. Adding mixture components increases flexibility but can cause overfitting; judge predictions using cross-validation, rather than interpreting every fitted component as a discovered population.^[ref]

Non-identifiability of shape from height and mass means that different external geometries can produce the same measured height and mass. The observation map from a body shape to those two numbers is many-to-one. A formula using only those inputs cannot distinguish shapes that the observations themselves do not distinguish. This is an identifiability issue in an inverse problem, independently of measurement precision.

An original family of homogeneous cuboids supplies an explicit proof. Fix height $H$, mass $M$ and density $\rho$, and define horizontal area $A=M/(\rho H)$. LetEvery real $t$ gives $ab=A$, the same height and the same mass. Its external surface area, however, isThe square section $t=0$ minimizes this family's area. At $t=\log 2$, the sides have ratio four and the lateral surface area is 25% larger. Height and mass remain exactly unchanged. This is a geometric construction, not a proposed anatomical model of a person.

With stipulated $H=1.8$ m, $M=80$ kg and $\rho =1000\mathrm{kg}{\mathrm{m}}^{-3}$, those two total areas are approximately $1.607$ and $1.986{\mathrm{m}}^2$. The Mosteller formula assigns both the same predicted body surface area, $2.00{\mathrm{m}}^2$, because its documented inputs are only height and mass.^[ref] No reduction of numerical rounding can make one identical prediction equal both different geometric areas.

Additional measurements and anatomical identifiability can change the problem. In this particular cuboid family, measuring the horizontal perimeter $P=2(a+b)$ identifies the area through $S=2A+HP$. That conclusion relies on the assumed geometry; a perimeter does not generally determine the full external surface of an arbitrary human body.

Validation must therefore ask whether the observations and model contain the shape information needed for the intended quantity. Repeated precise height and mass measurements constrain the inputs. Independent geometric measurements or a validated restriction on allowable shapes constrain the missing anatomical information.

Nonregular identification at a flat mean map occurs when different parameter values give different probability distributions, yet the first derivative of the observable mean vanishes at a parameter of interest. Identifiability is a property of the entire parameter-to-distribution map; a first-order sensitivity calculation can miss it.

Consider an original statistical model with independent observationsThe cubic mean map is a strictly increasing function, so equality of the normal distributions implies equality of $\theta$. The model is globally identifiable, including at $\theta =0$. Nevertheless, the single-observation score function and Fisher information areThus $I(0)=0$ does not imply nonidentifiability. The rank is zero at the origin and one at every nonzero nearby point. This is precisely why a regular-point assumption matters: Rothenberg's local identification criterion assumes constant information-matrix rank in a neighborhood.^[ref]

Maximum likelihood estimation gives $\hat{\theta }=\mathrm{cbrt}(\overline{Y})$, using the real cube root. At the true value zero, write $\overline{Y}=Z/\sqrt{n}$ with a standard normal random variable $Z$. ThenThis is an exact sampling distribution identity for every $n$, not merely a convergence in distribution statement. The estimation error has scale $n^{-1/6}$ and a nonnormal shape. At a fixed nonzero $\theta$, the usual delta method instead gives asymptotic variance $1/(9n{\theta }^4)$; that approximation cannot be extended uniformly through zero.

An exact confidence interval through a cubic mean map follows by applying the strictly increasing function $\mathrm{cbrt}$ to both endpoints of the ordinary known-variance confidence interval for the mean:Here $z_p$ is the quantile function of the standard normal distribution. The transformed interval has exact coverage $1-\alpha$ for every $\theta$. When $n=64$ and the observed sample mean is zero, the 95% interval is approximately $[-0.626,0.626]$. Multiplying $n$ by 64 halves its width at that observed mean. A first-order interval based on dividing by the zero mean-map derivative would fail instead.