Week 3. Performance Measurement, Monitoring, and Employer Learning

Learning Objectives¶

By the end of this week, students should be able to distinguish production from its measurement; explain how repeated signals change employer beliefs; separate learning about a worker from changes in the worker’s productivity; interpret objective measures, subjective ratings, and monitoring records without treating any as ground truth; and design a study that measures both a targeted performance margin and an independently recorded outcome. Students should also be able to identify what a monitoring or feedback intervention actually changes, select an appropriate comparison and inferential unit, and state which welfare and selection questions remain unanswered.

Research deliverable: a two-page measurement-validation plan with two distinct outcome families, a worker-welfare margin, and an information timeline.

Opening Orientation¶

Central question: How do firms learn about ability, effort, and match quality when observed performance is incomplete or strategically produced?

A firm introduces a dashboard. Recorded idle time falls, supervisor ratings rise, and employee turnover changes. Has the firm learned more about its workers, induced greater effort, reassigned difficult tasks, changed how time is coded, or made the job less tolerable? These are different economic explanations. A larger personnel dataset does not separate them by itself.

This week opens the information problem inside the employment relationship. Week 2 followed people into jobs; Week 3 asks what an employer can infer once work begins. The object is not a universal productivity score. It is the sequence linking production, observation, interpretation, feedback, and organizational decisions. A record can be accurate as an administrative event and still be a poor measure of the economic construct a paper needs.

The contemporary personnel-economics review by Hoffman and Stanton provides the broad research map, while Benson and Shaw explain why evaluation is one managerial function among several. We use these reviews as orientation, not as substitutes for studying concrete designs Hoffman & Stanton, 2025Benson & Shaw, 2025. The three required research readings examine different parts of the problem: Kahn–Lange on learning versus changing productivity; de Janvry and coauthors on strategically produced evaluation signals; and Bernstein–Li on who receives existing performance data. The remaining readings create pathways for student projects rather than an impossible compulsory list.

Core Points¶

Bridge¶

Recruitment creates an initial workforce and an initial information set. Probation and early reviews update that information but also affect assignment, dismissal, and who remains visible in the data. Carry Week 2’s selection discipline forward: performance observed only among retained workers is not the same outcome as total contribution by the baseline workforce.

Keep three boundaries clear. We study ratings before deriving optimal compensation contracts; we study evaluator heterogeneity without attempting the full causal-manager-effect lecture; and we distinguish learning about a fixed type from human-capital accumulation without replacing the later training and career-ladders week.

Imagine an employee who completes the same work before and after a new review form, but receives a higher score afterward. The score changed; productive capacity may not have. Now imagine that the form makes one visible task especially salient, and the employee reallocates time toward it. Production may change too, but the score alone cannot show which work was displaced. Finally, a more precise audit could help the employer learn about unchanged performance. These are recording, behavior, and information changes with different implications.

A useful comparison pairs the routine measure with a second outcome that could contradict it: completed work with blinded quality audits, or activity logs with rework and employee-reported pressure. Ask who observes each measure, when they receive it, and what decision it can affect. These questions connect the Bridge intuition to the Field Core models and research designs.

Field Core¶

1. Begin with the production object, not the dashboard¶

A useful teaching decomposition, not an estimated production function from a cited paper, is

Indices $i$, $j$, and $t$ identify the worker, job/task, and period. Here $q$ is quality-adjusted production on a comparable scale, $\theta$ is productive capacity, $\mu$ is worker–job match, $a$ is effort, $d$ is task difficulty, and $u$ collects common operating conditions; $\epsilon$ is the remaining production disturbance. The additive form is deliberately simple. In many jobs these inputs are complementary, and neither output nor effort has a natural common cardinal scale.

The observed record can follow a different equation:

The version index $v$ denotes a sensor, rubric, software, or coding regime; $\lambda_v$ is the sensitivity of the recorded index to production; $r$ denotes the evaluator; $b$ is evaluator calibration; $\zeta$ is strategic reporting or visibility; $\nu$ is residual recording noise; and $O$ indicates that the record is observed. A rating scale can additionally discretize this latent index. A move from rating 2 to rating 3 should not automatically be valued like a move from 4 to 5.

This decomposition gives students a practical data request. For a sales measure, request prices, returns, customer mix, territory assignments, and product availability. For a service-time measure, request queues, complexity, quality checks, and rework. For a performance rating, request the rubric version, rater, review date, period covered, and who saw the rating before each pay or assignment decision. For an attendance record, define whether approved leave, training, remote work, or system downtime is coded as absence.

An input such as calls made can be informative without equaling output. Revenue can change through price rather than quantity; time saved can shift into unmeasured support rather than production; customer ratings can reflect customer composition. The correct response is not to reject these records but to state what each measures and add a second outcome family capable of challenging the proposed interpretation.

Use the table as a data dictionary, not a ranking of “good” versus “bad” outcomes. A useful variable has an explicit economic interpretation, denominator, recording rule, and information date.

Two common traps. Standardizing scores within each evaluator can erase real quality differences as well as generosity. Conditioning on post-reform tasks can remove the assignment response that the reform caused. Keep raw measures and report what comparison each normalization targets.

Application anchors: Kahn & Lange, 2014Frederiksen et al., 2020Bernstein & Li, 2026Takahashi et al., 2021.

Worked case-mix example. Suppose two employees each handle ten tasks. One handles eight easy tasks worth one completed unit each and two hard tasks worth two units each; another handles two easy and eight hard tasks. Raw completion counts both equal ten, while difficulty-adjusted contributions are 12 and 18 under the specified hypothetical weights. Those weights require economic justification. Moreover, if the intervention changes assignment, controlling for post-intervention task difficulty can remove part of the policy’s effect. Report the total assignment-inclusive effect and, separately, a clearly defined fixed-case-mix comparison. Neither should be mislabeled as the other.

2. What does it mean for an employer to learn?¶

Start with a deliberately restrictive signal model. A worker has fixed ability $\theta\sim N(\mu_0,P_0)$. After accounting for effort and task conditions, the firm observes $s_t=\theta+\nu_t$, with mean-zero normal noise of known variance $R>0$, independent across periods and independent of the initial type. Let $\mu_t$ and $P_t$ be the posterior mean and variance after signal $t$, and $K_t$ the gain placed on its surprise. Posterior updating is

The new observation matters more when it is precise relative to the prior. A firm uncertain about a novice can revise its belief sharply; a firm with a long reliable record may put little weight on one surprising evaluation. This is a model of information, not a statement that managers actually compute Gaussian posteriors.

Numerical illustration. With prior mean zero and variance one, a signal of two produces posterior mean 0.4 and variance 0.8 when its noise variance is four. With noise variance one, the same signal produces posterior mean one and variance 0.5. The worker’s productive type has not changed between these examples. Only signal precision has changed.

The assumptions reveal the research agenda. Does the employer know task difficulty? Is effort separately observed? Are successive scores independently noisy or copied from past ratings? Is a new sensor changing precision or changing the activity measured? Do the worker, supervisor, and outside employers see the same information? Calling a variable a signal does not settle these questions.

Repeated ratings improve precision less when raters share errors. For $R_a$ equal-variance raters, common pairwise error correlation $\rho$, and individual error variance $\sigma^2$,

Four independent unit-variance ratings yield variance 0.25. With correlation 0.75 they yield 0.8125. A shared systematic bias is not averaged away at all. These are covariance identities under the stated assumptions, not estimated effects of adopting multirater evaluation.

Ockenfels, Sliwka, and Werner combine a model with controlled laboratory evidence on multirater evaluations and incentives. Use the study to ask when aggregation becomes more informative, not to claim that more reviewers always solve personnel-evaluation problems Ockenfels et al., 2025. The organizational design question is which independent information each additional reviewer brings and what reporting incentives each faces.

3. Employer learning is not the same as rising productivity¶

The fixed-type model becomes misleading when productive capacity itself changes. A minimal alternative is $\theta_t=\theta_{t-1}+\omega_t$, where $\omega_t\sim N(0,Q)$, $Q\geq0$, independently across periods and independently of initial ability and observation noise. Before a new observation, uncertainty is $P_t^-=P_{t-1}+Q$; after it,

Now the employer can remain uncertain even after many observations because the target moves. Figure Figure 1 isolates that distinction under the hypothetical signal model. Changing knowledge, health, technology, job assignments, or motivation can all invalidate a fixed-type approximation. A decline in forecast errors can indicate learning; changing performance can indicate productivity evolution; wages combine both with pay rules and outside opportunities.

The classic employer-learning papers teach how to exploit differences between information observed by researchers and information available to firms. Farber and Gibbons derive restrictions linking wages and researcher-observed ability correlates as experience accumulates. Importantly, their model can imply a schooling coefficient that stays constant with experience. Altonji and Pierret study schooling and difficult-to-observe ability proxies in an employer-learning/statistical-discrimination framework. Their test jointly follows experience interactions with schooling and a harder-to-observe productivity proxy: increasing weight on the proxy accompanies declining weight on schooling in that conditional specification. This is a different conditioning argument from Farber–Gibbons, not a prediction that every learning model has a falling schooling coefficient Farber & Gibbons, 1996Altonji & Pierret, 2001. Lange then uses a model to estimate how rapidly employer uncertainty is resolved; that is not a direct audit of individual managers’ updating rules Lange, 2007.

Required anchor: Kahn and Lange. Their twenty-year single-firm panel combines performance measures and earnings in a dynamic model that allows both employer learning and changing productivity. The additional performance information helps distinguish mechanisms that wage data alone struggle to separate Kahn & Lange, 2014. The useful lesson is the identification architecture: which serial covariances and information restrictions distinguish persistent productivity, changing productivity, and forecast error? Ratings remain noisy measures rather than observed true ability. Students should explain what a different measurement process would do to the decomposition.

A practical project should therefore write an information-availability timeline before estimating a wage regression. Record when work occurred, when a score was entered, when the employer received it, and when pay or assignment was set. A later score can help a researcher assess earlier expectations without having been available to the employer at that time. Using that later score as an actual earlier policy predictor would be leakage. These are different uses of the same column.

4. Objective and subjective measures can complement one another¶

“Objective” usually means recorded by a rule; it does not mean complete, manipulation-proof, or independent of task allocation. “Subjective” means judgment enters; it does not imply the information is useless. The empirically useful question is whether a rating adds information about relevant performance beyond the existing measured outcomes and whether that information survives changes in evaluator and context.

Takahashi and coauthors study car salespeople and examine information in subjective ratings beyond contemporaneous sales. The setting illustrates why relationship building or assistance to others may be missing from a narrow sales count Takahashi et al., 2021. Predicting future sales is a useful validation exercise, but it does not by itself establish an unbiased ability measure: ratings may affect opportunities, effort, customer assignment, or retention, which then affect later sales.

Evaluator heterogeneity. Frederiksen, Kahn, and Lange combine personnel data and a model to distinguish supervisor leniency from genuine managerial ability and firms’ information about it. Their evidence does not support treating all high-rating supervisors as merely lenient Frederiksen et al., 2020. This is an ideal paper for teaching why “remove the supervisor fixed effect” is not an innocent measurement correction. One could remove useful variation in coaching or allocation along with rating generosity.

A workable validation design might use blinded independent assessments, crossed raters evaluating the same tasks, or externally recorded quality outcomes. Rater rotation is helpful only if its assignment process and other channels are defensible. A supervisor who changes ratings may also change tasks, feedback, morale, and promotion support. Rotations are not automatically valid instruments for a score.

Kusterer and Sliwka’s online experiment varies features of evaluation incentives and information and studies the informativeness of subjective ratings alongside evaluator social preferences Kusterer & Sliwka, 2025. Keep the experimental variation separate from measured preference heterogeneity. For an applied firm project, this suggests observing both the information a rater receives and the consequences of the rating for another person, rather than modeling rating error as homogeneous noise.

Baker, Gibbons, and Murphy offer the theoretical bridge: subjective information can complement incomplete objective measures within an incentive relationship. We use this motivation now; the full contractual enforcement problem belongs in Week 4 Baker et al., 1994.

5. Evaluation changes how the signal is produced¶

A worker may increase productive effort, devote effort to visible tasks, seek favorable evaluators, or influence the interpretation of ambiguous work. These are behavioral responses to the evaluation process, not merely errors imposed on a fixed outcome.

Required anchor: de Janvry and coauthors. The field experiment with local civil servants in China changes uncertainty about the evaluator’s identity. It studies evaluator-specific influence activities and work behavior under subjective evaluation Janvry et al., 2023. Its central teaching contribution is an intervention on the evaluation process itself, rather than the addition of another noisy productivity proxy. Students should separate the randomized treatment from particular proposed behavioral channels, and evaluate what the measured performance outcomes capture.

A useful protocol for reading this and related studies asks: What information or rule changed? Was pay also changed? Did task priorities change? Were administrative records measured consistently in both arms? Which behavior was observed independently of the evaluator? Which actor’s preferences determine the score? The same protocol applies in firms, schools, and professional systems without requiring the same institutional interpretation everywhere.

Career incentives already make performance endogenous even when the current wage is fixed. Holmström’s dynamic career-concerns framework explains why workers may invest effort in shaping beliefs about ability Holmström, 1999. The distinction for this week is between a more precise signal and a differently produced signal. Week 4 will ask whether the resulting effort allocation is desirable and how explicit contracts should respond.

6. Monitoring is both an observation technology and an intervention¶

Monitoring can change information, detection, salience, perceived trust, coordination, or discretion. An empirical study should identify the component actually varied instead of attaching all these channels to a single treatment dummy.

Detection is not incidence. If false positives are absent, a simple measurement model gives

In a hypothetical example, latent misconduct falls from 0.10 to 0.06 while detection rises from 0.25 to 0.75. Recorded incidents rise from 0.025 to 0.045. A worse administrative number can therefore coexist with improved behavior. With false positives, the additional error term must also be modeled. The practical remedy is a stable independent audit or a design that separately identifies detection, not a more elaborate regression on the same detection-dependent outcome.

Pierce, Snow, and McAfee study monitoring-technology adoption in restaurants, examining recorded theft and sales. It is a useful multiple-outcome, staggered-adoption application, not a randomized technology deployment Pierce et al., 2015. Students should ask how adoption timing, store trends, spillovers, and observation rules affect the interpretation, and how a modern group-time comparison would define the target rather than rerunning a generic before–after regression Callaway & Sant'Anna, 2021.

Bernstein’s transparency-paradox study provides a different production setting in which privacy and visibility affect organizational learning and behavior Bernstein, 2012. Falk and Kosfeld’s control experiment is a laboratory principal-agent setting with a minimum-performance restriction, not a workplace-surveillance rollout Falk & Kosfeld, 2006. Read them as distinct mechanisms and evidence types. Neither licenses a universal claim that monitoring helps or harms workers.

Recent monitoring application: Phipps. The 2026 article studies exogenous variation in unannounced teacher observations and connects monitoring to pedagogy and student outcomes Phipps, 2026. The immediate reading task is to reconstruct the observation-assignment rule before asserting which comparisons are quasi-random. Do not relabel it a randomized trial from the title. Its data note identifies proprietary microdata and a code/data-description archive. This is useful for thinking about independently measured service outcomes, but not a guaranteed public-microdata classroom replication.

7. Who receives the information? Feedback to workers versus supervisors¶

Firms can collect a measure without sharing it with workers; supervisors can filter, contextualize, delay, or selectively communicate it. Giving workers direct access therefore changes an information institution, even when the underlying data already exist.

Required anchor and lab motivation: Bernstein and Li. Their field experiment gives frontline mechanics direct access to their own and peers’ performance data, limiting supervisors’ exclusive intermediation while leaving supervisors informed. Four of eleven work centers were assigned treatment. The article also describes a company/union constraint on the number of employees affected; the count alone does not establish that every four-center subset was admissible. Our lab explicitly imposes uniform complete randomization as a teaching design. The paper distinguishes productive, support, and nonproductive time; reduced nonproductive time did not establish a corresponding overall productive-time increase Bernstein & Li, 2026. That distinction is the lesson, not a license to convert time categories into welfare or infer independently randomized managerial mechanisms.

The case motivates three separate questions. Did knowledge improve? Did activities change? Did the changed activities improve output, quality, or worker welfare? An intervention can answer the second without fully answering the first or third. Since own and peer information are delivered together, the study does not automatically separate self-monitoring from comparison with colleagues.

Blanes i Vidal and Nossol study relative-performance feedback without introducing a new monetary prize, but workers still faced an existing piece-rate environment Vidal & Nossol, 2011. Rilke and coauthors study input-based relative feedback in sales, compared with existing information on one’s own inputs. Responses among initially low performers show why inputs, outcomes, and conversion efficiency deserve separate columns Rilke et al., 2025. Input feedback can tell someone what behavior to change; that does not imply the same response to outcome ranks.

Factorial design thought experiment. Propose independent randomization of access to one’s own history and access to peers’ histories. Add an unchanged blinded quality measure. A further supervisor-feedback arm can test whether interpretation matters beyond raw data access. This is a proposed design, not a claim that the cited papers implemented this full factorial. Define treatment at a level where peers’ access cannot silently contaminate controls, and measure staff concerns about privacy or pressure separately from production.

8. Building a usable personnel-data panel¶

The minimum useful unit is often worker × task/job × evaluator × period, not simply worker-year. Preserve stable identifiers; distinguish establishment from firm; map review periods to the output they cover; preserve rubric and software versions; and flag when a record was altered after a decision. Retain raw ratings as well as any standardized score so the measurement change remains auditable.

Add a visibility ledger: recorded by whom, available to whom, and available when. Internal pay records reveal compensation decisions, not automatically employer beliefs. A researcher-observed test may be known to the firm indirectly through correlated information. A missing rating may indicate exit, exemption, leave, system failure, or selective evaluation. Those are not exchangeable zeros.

The BLS National Longitudinal Surveys are an accessible starting point for wage histories and employer-learning applications; the public-use route and restricted-access tiers are documented separately U.S. Bureau of Labor Statistics, 2026. The Linked Personnel Panel links employer and worker perspectives on HR practices and job quality, with access governed by the IAB’s product-specific conditions Institute for Employment Research, Research Data Centre, n.d.. Neither should be advertised as a public source of every firm’s minute-level output and supervisor ratings. A partner firm’s records are a separate access proposition.

The archive linked to the de Janvry article provides an optional replication route, subject to inspecting actual files and permissions Janvry et al., 2023. The Phipps archive reference concerns code and a data description, not freely downloadable original school microdata Phipps, 2024. Bernstein–Li and Ockenfels and coauthors advertise supplemental materials; those listings are not proof that all original variables can be freely redistributed. Our guaranteed lab therefore uses explicitly synthetic records.

Public documentation, public code, public microdata, and permission to redistribute are different access states. Do not request access or download restricted data automatically. The mandatory lab is offline and synthetic.

Minimum panel keys: stable worker ID, job/task ID, establishment/team ID, rater ID, measurement version, work date, recording date, information-release date, and decision date. Keep the baseline worker roster even when ratings subsequently disappear. Store confidential linkages separately from analysis extracts.

9. From a compelling dataset to an identified mechanism¶

Independent outcomes. A second outcome family should challenge the first rather than restate it. A supervisor’s overall score and that same supervisor’s narrative sentiment share a measurement source. Better contrasts include counts versus blinded quality audits; time use versus completed work and rework; evaluator scores versus external customer outcomes; employer profit versus worker-reported pressure and predictable hours. No single pair is universally sufficient, but the failure channels should differ.

Leave-out and time separation. Consider $y_{it}=\theta_i+e_{it}$ with mean-zero transitory noise that is independent across periods and independent of $\theta_i$, with common variance $\sigma_e^2$. If a worker score uses all $T$ observations including the focal record,

Leaving the focal observation out removes this mechanical covariance under independent errors. It does not remove serial correlation, common task shocks, endogenous peer assignment, or future-information leakage. A strictly historical score is appropriate for a prospective decision, while a future independent measure can be used for retrospective validation with a different interpretation. Cross-fitting must respect worker, rater, team, and time dependence rather than randomly shuffling rows.

Kline, Saggio, and Sølvsten provide methods for noisy fixed-effect variance components. Their leave-out correction is not simply the deletion of one observation from a worker average, and neither approach by itself identifies causal evaluator effects Kline et al., 2020. Students should state the estimation target and error dependence before choosing a correction.

Selection. Follow the baseline population after a monitoring change. Report retention or observation probabilities alongside performance. The contribution to firm production of someone who exits can be defined as zero for a fixed employer-accounting target; their unobserved potential quality in that job is not observed zero. An analysis of ratings among survivors targets a selected group. Lee-style bounds require the relevant monotone-selection and assignment assumptions; balanced average attrition does not establish monotonicity Lee, 2009.

Few assignment units. A study with many worker-days but eleven independently assigned centers does not contain thousands of independent treatment assignments. In our teaching design, exactly four centers are selected uniformly from eleven. Define center outcome changes $\Delta\bar y_c$ and estimate an equal-center-weighted effect:

This differs from a worker-weighted target if center sizes differ. Under the sharp null of no effect on any observed unit, evaluate the statistic under all $\binom{11}{4}=330$ center assignments. This is not a generic test of a weak average-effect null, and it is valid for the stated complete-randomization design, not an unknown blocked or constrained assignment. Permuting individual worker-days is wrong. For an empirical replication, use the paper’s actual randomization protocol and prespecified outcome family.

10. Research opportunities that build on this week’s evidence¶

The following are proposed research directions, not claims that a topic is unstudied. Each begins with an information or measurement distinction and a feasible empirical target.

Changing evaluator and sensor regimes. A new automated score, review form, or software version can alter both detection and worker behavior. Seek a parallel-run period, where old and new measures coexist, plus an independently audited outcome. The opportunity is to estimate the role of measurement changes in an apparent productivity shift, not to declare the new score true. Hold full organizational AI adoption for Week 9.

Who sees performance information? The direct-access, ranking-feedback, and evaluator-identity studies suggest experiments that independently vary information precision, recipients, and interpretation. Pair knowledge questions with task-level outcomes. Investigate which workers benefit from additional information rather than assuming uniform responses Bernstein & Li, 2026Janvry et al., 2023Rilke et al., 2025.

Learning about a moving target. Combine repeated performance assessments, task assignments, and pay histories to test a fixed-type learning model against productivity evolution. A training or rotation intervention can change both skill and information, so a clean design needs an outcome or timing restriction that separates them. The ambition is an identified decomposition with sensitivity analysis, not naming an estimated residual “ability” Kahn & Lange, 2014.

Measurement and worker welfare. Retain work-quality measures while adding pressure, autonomy, privacy, predictable scheduling, or willingness to remain. A firm can improve a targeted metric while shifting costs to employees. A study need not monetize all dimensions to avoid treating the firm’s objective as social welfare. Confidential surveys and protected analysis access should be planned before collection, not improvised afterward.

Multirater evaluation under correlated information. Use common tasks, independent assessment assignments, and known visibility rules to separate calibration from shared errors. The new outcome could be decision accuracy at a fixed review cost, or whether different groups of workers receive equally informative evaluations. Descriptive gaps or rater heterogeneity alone do not identify unfair treatment Ockenfels et al., 2025Kusterer & Sliwka, 2025.

This is a reading guide to the evidence, not a claim that every study implements the same causal design. Published issue years are used where the online-first year differs.

Methods papers play narrower roles: noisy variance components Kline et al., 2020, selection bounds Lee, 2009, and explicit comparison groups in staggered adoption Callaway & Sant'Anna, 2021. None replaces the institutional assignment argument.

Research Lab¶

Reproduce — a bounded design reconstruction¶

The primary reading is Bernstein and Li, with a clearly labeled offline synthetic design reconstruction. The article advertises supplemental material, but its original microdata have not been downloaded or executed for this pack. An optional empirical route may be added only after checking what the release actually contains and permits Bernstein & Li, 2026.

The included lab creates eleven centers with four assigned treatment, different center sizes, and repeated worker observations. All workers, outcomes, parameters, and treatment magnitudes are invented. Its exhaustive 480-minute time budget is a teaching simplification, not an asserted replication of the original firm’s accounting rules. Students estimate center-level changes in nonproductive, productive, and support time plus an independent quality measure. They then run exact center-assignment inference for the prespecified primary endpoint.

Diagnose — distinguish three explanations for a better score¶

Students examine an intervention that reallocates recorded time without a direct productive-time or quality effect in the synthetic data-generating process; a separate recording-rule change that raises a score without changing a blinded audit; and a Bayesian-learning exercise in which the employer’s uncertainty changes while the production model is explicitly specified. Additional diagnostics compare independent versus correlated ratings and demonstrate own-record leakage in a worker average.

The exercise requires a written answer to: Which effect is identified by randomization? Which difference is merely a measurement identity? Which result follows from the assumed signal model? Which welfare questions remain open? A non-significant quality effect does not establish equivalence, and a randomized dashboard does not independently randomize its behavioral channels.

Transfer — a measurement-validation design¶

Write a two-page proposal for a workplace measurement or feedback reform. Specify the baseline population, unit of randomization or quasi-exogenous variation, who sees which information, primary measure, independent outcome family, and worker-welfare outcome. State one plausible alternative explanation and the result that would make you change your interpretation. Add a data dictionary with timing and access restrictions. The lab handout gives the run order and diagnostics; the transfer memo template structures the proposal and data dictionary. The requirement is a credible design, not a completed empirical paper.

Methods Box¶

Implementation note: uncertainty from estimating a historical performance score is distinct from endogenous signal production. Cross-fitting, shrinkage, resampling, and fixed effects solve different problems. Choose the correction only after stating which problem is present.

Reading Ladder And References¶

Required (three papers). Kahn and Lange (2014): explain the restrictions separating employer learning from productivity evolution. De Janvry and coauthors (2023): reconstruct the evaluation intervention and the behavioral margins it can identify. Bernstein and Li (2026 issue; online 2025): distinguish data access, changed activities, and output claims Kahn & Lange, 2014Janvry et al., 2023Bernstein & Li, 2026.

Foundations and identification follow-up. Farber–Gibbons, Altonji–Pierret, and Lange provide the wage-learning lineage. Read them for their distinct information restrictions, not a common slogan. Kline–Saggio–Sølvsten, Lee, and Callaway–Sant’Anna are targeted methods readings for noisy components, selected outcomes, and staggered adoption, respectively Farber & Gibbons, 1996Altonji & Pierret, 2001Lange, 2007Kline et al., 2020Lee, 2009Callaway & Sant'Anna, 2021.

Rotating research presentations. Choose one evaluator paper (Frederiksen–Kahn–Lange, Ockenfels–Sliwka–Werner, Kusterer–Sliwka, or Takahashi et al.) and one monitoring/feedback paper (Phipps, Pierce et al., Bernstein, Blanes i Vidal–Nossol, or Rilke et al.). Each presentation must give the data source, variation, information change, independent outcome, and an interpretation limit Frederiksen et al., 2020Ockenfels et al., 2025Kusterer & Sliwka, 2025Takahashi et al., 2021Phipps, 2026Pierce et al., 2015Bernstein, 2012Vidal & Nossol, 2011Rilke et al., 2025.

Bridge readings, not a second contracts lecture. Holmström, Baker–Gibbons–Murphy, Falk–Kosfeld, and Duflo–Hanna–Ryan show why observation, beliefs, and rewards interact. The camera-and-attendance-pay intervention in Duflo and coauthors is specifically a bundle, not evidence about monitoring alone; this chapter uses only that design distinction, and any reproduction of the original structural calculations must first consult the journal erratum Holmström, 1999Baker et al., 1994Falk & Kosfeld, 2006Duflo et al., 2012.

Teaching route: use a substantive lecture plus a separate research-lab discussion, or two meetings. Do not compress the uncertainty, measurement, and selection distinctions into a list of paper titles. The breadth of the bibliography is a resource for projects; only three papers are required.

Exercises And Discussion Prompts¶

1. A monitoring reform raises recorded safety incidents but reduces independent audit failures. Give a measurement explanation, a behavioral explanation, and one additional datum that would discriminate between them.

2. Derive the two posterior updates in the numerical example. Which object changes when signal precision improves? Why does this not identify a causal effort response?

3. Explain why four raters with strongly correlated errors may add little information. Propose a reviewer assignment rule that could make the marginal information content measurable.

4. A supervisor fixed effect predicts both high ratings and high worker output. Explain why neither pure leniency nor causal managerial ability follows automatically.

5. Reconstruct one classic employer-learning paper’s information assumptions. Which prediction would fail if the firm already observed the researcher’s ability proxy?

6. Design a feedback experiment that separates own-information access from peer comparison. Specify contamination channels and the assignment unit.

7. In the synthetic lab, compare a change in recorded time with a change in quality. Explain why the point estimates and sharp-null tests answer narrower questions than “does the reform improve welfare?”

8. Deliver the two-page transfer proposal and a measurement dictionary with two independent outcome families, a welfare measure, and a falsifiable alternative explanation.

Reproducibility And Code Lab Note¶

Download the teaching repository (ZIP), or clone the repository. Keep its folder structure and open books/special-topic8-organizational/labs/03-performance-measurement-monitoring-and-employer-learning/; the lab README supplies the run instructions. Weeks 1–3 use the shared plotting module supplied with the repository.

The Week 3 lab handout guides Reproduce, Diagnose, and Transfer. From labs/03-performance-measurement-monitoring-and-employer-learning/, run:

ENV_NAME=research bash smoke.sh

The mandatory Mode A is synthetic design reconstruction, with empirical_replication: false. The standard-library core invents 76 workers and 1,216 worker-period records across eleven centers; its 480-minute accounting rule and all effect sizes are teaching assumptions. The smoke executes assignment and schema checks, enumerates all 330 possible center assignments, verifies time accounting, posterior updating, correlated-rater variance, detection arithmetic, and own-record leakage, and compares deterministic reruns. Plotting uses the existing Matplotlib environment. It needs no network, restricted input, or credential.

The optional Mode B original-release route is omitted. A publisher supplement listing does not establish original-data availability, redistribution permission, or successful empirical replication. The instructor-only file contains separated synthetic truth, not confidential personnel data.

Rebuild the chapter figure from this book directory after the lab has generated its CSVs:

conda run -n research python assets/scripts/build-week3-learning.py

The script copies the lab’s generated uncertainty data to assets/data/03-learning-uncertainty.csv and produces the PNG/PDF in assets/figures/. Parameters, paths, and synthetic provenance are explicit; no empirical chart is copied.

Slide Companion Note¶

The Week 3 slide deck (PDF) follows the production/recording distinction, signal models, required paper designs, monitoring and feedback comparisons, and research lab. The Beamer source uses the finished Week 1–2 style. The full lecture supports two meetings or a lecture plus lab discussion; the chapter’s longer evidence and reading maps serve as handouts.

Bridge Forward¶

A firm must first decide what it can learn and measure. It must then decide what to reward. Week 4 adds the compensation, risk-sharing, multitasking, and relational-contract problem. Carry this week’s discipline forward: attaching stronger rewards to a number is not the same thing as increasing the value of the underlying work.