# Testing Firm Conduct

Marco Duarte
Lorenzo Magnolfi  Christopher Sullivan
Department of Economics, University of Wisconsin, Madison, WI 53706; Duarte:
<EMAIL_ADDRESS>Magnolfi<EMAIL_ADDRESS>Sullivan:
<EMAIL_ADDRESS>We would like to thank IRI. for making the data
available. All estimates and analysis in this paper, based on data provided by
IRI. are by the authors and not by IRI.

(This version: January, 2021
First version: November, 2020 )

###### Abstract

Understanding the nature of firm competition is of first order importance.
Researchers have used different procedures to test alternative models of firm
conduct. In this paper, we formally compare the properties of these
procedures, contrasting those designed for model assessment with those that
perform model selection. In the absence of data on marginal costs, tests rely
on a moment condition that must be formed using valid excluded instruments,
e.g. demand rotators. We extend the intuition in b82 and show that the
testability condition in bh14 requires - in a parametric environment - that
the two candidate models generate different projections of markups on
instruments. Without model misspecification, we show that a partial ranking in
power exists among testing procedures in this setting. We then turn attention
to the empirically relevant setting where either demand or cost is
misspecified. Here we discuss the limitations of procedures designed to
perform model assessment relative to model selection. With enough data, model
assessment procedures will reject true models of conduct even for a small
amount of demand or cost misspecification. However, the test developed in rv02
may still be capable of selecting the true model. We next provide guidance on
key aspects of the implementation of the RV test. In doing so we highlight the
pitfalls of not using excluded instruments, the relation between degeneracy of
the test and weak instruments for testing, the tradeoffs in being flexible in
specifying instruments, and the implications of estimating demand with and
without supply moments for testing.

##  1 Introduction

Firm conduct is both of independent interest for researchers (e.g. to detect
collusive behavior, characterize conduct of non-profit firms, or determine the
competitive effects of horizontal ownership), and a fundamental input into
structural models of imperfectly competitive markets that are used to evaluate
policy in many realms (e.g. competition enforcement, environmental regulation,
trade policy). Often the true model of conduct is unknown. Thus, researchers
typically perform econometric tests to evaluate a set of candidate models that
are motivated by theory.

We consider the setting where theory suggests alternative models of conduct.
Examples of this setting in the industrial organization literature include
investigations into the nature of vertical relationships, whether firms
compete in prices or quantities, collusion versus competitive pricing, intra-
firm internalization, common ownership, and nonprofit conduct. Papers in this
area have used a variety of testing procedures, some of which are designed to
perform model assessment and others for model selection. Model assessment
independently pits each model against a set of alternatives, and uses the data
to make a determination on whether that model can be rejected. Instead, model
selection evaluates which of the candidate models better fits the data.
Although several approaches co-exist in the literature, to our knowledge there
has been no systematic comparison of their properties.

In this paper we compare the econometric properties of four commonly used
approaches to test firm conduct in a static model of supply and demand. These
four approaches are: an estimation based (EB) procedure where testing is
conducted as a by-product of estimation, a procedure that closely resembles an
Anderson-Rubin test (AR), a Cox test, and a Rivers-Vuong test (RV). The first
three are procedures designed for model assessment; the fourth is designed for
model selection. We evaluate the properties of these procedures, considering
both environments where all elements of the model are well-specified and also
environments where some elements (such as demand or costs) may be
misspecified. While the analytical results are obtained for the setting where
the researcher tests two competing model, we show how our preferred testing
procedure naturally extends to an arbitrary number of candidate models.

We start our analysis in an ideal setting where the researcher has some
information on either true marginal costs or markups, as it is the case in
n01. In this environment, different hypotheses on conduct can be evaluated by
comparing the distributions of markups that they generate with the observed
truth. This setting serves as a benchmark to illustrate the difference between
model selection and model assessment.

More commonly, true markups are not observed, and we provide assumptions under
which testing is possible in this case. We start from the intuition in b82,
which we extend to a standard setting with differentiated products and two
hypotheses on conduct. We then formalize the connection between the
nonparametric environment in bh14 and this parametric setting. In doing so, we
show that rejecting a wrong model of conduct in a large sample requires that
model to generate different predicted markups (i.e. markups projected on the
instruments) than the true model. This contrasts to the setting where true
markups are observed and a model is falsified if it generates different
markups than the true model. So when markups are unobserved, all of the four
testing procedures that we examine need to rely on the same moment condition
formed with excluded instruments.

Next, we consider these four tests in a setting where markups are measured
without misspecification. All tests are consistent and have the right size
under these conditions. Their power, however, is a function of the distance
between the distributions of predicted markups for each candidate model and
the true distribution of predicted markups. Using local power analysis, we are
also able to provide a partial ranking between the four tests in this setting.
Cox tests are the most powerful, and AR is weakly less powerful than EB. In
fact, AR becomes increasingly less powerful as the number of instruments
increases.

We then turn attention to the setting where either demand or marginal cost may
be misspecified. Importantly, we show that misspecification - a likely
occurrence in most empirical applications - alters the properties of these
tests. In this setting, tests designed to do model assessment reject the true
model of conduct for a large enough sample size. We also show that the RV
approach may allow the researcher to conclude in favor of the true model. We
formalize that, in the presence of misspecification, the test statistics for
the four tests depend on both bias and noise. Here, we define bias as the
distance between the distribution of predicted markups with and without
misspecification, for the true model of conduct. Noise arises from both the
variance of unobservables and sample size. If bias is low and the sample size
is large enough, RV is the only test which concludes in favor of the true
model of conduct, making it robust to mild misspecification. In fact, if the
other tests conclude in favor of any model, it is due to noise. Given the
progress made on demand estimation, and the increasing availability of data,
we believe that such low-bias environments are likely to be prevalent in many
applications, making RV an appealing testing procedure.

Overall, our results suggest that a researcher may want to adopt a model
selection perspective when testing for firm conduct. Thus, we provide guidance
on key aspects of the implementation of the RV test. First, we consider the
choice of instruments. Motivated by examples in the literature, we show that
conducting RV tests without excluded instruments can yield misleading results.
We also discuss the choice of excluded variables and the tradeoffs in flexibly
specifying the instruments from these variables. Second, we motivate our
choice of weight matrix. Third, we explore the implications of estimating
demand with and without supply moments for testing. Fourth, we discuss the
interpretability of RV test results. In particular, model selection only
establishes that a model provides a better approximation of the truth than an
alternative model. Given that one may be concerned both models are far from
the truth in an absolute sense, we propose that a researcher supplement the
results from an RV approach with specific estimation exercises that speak to
the absolute distance between each candidate model and the data. Finally, we
discuss how researchers, using the procedure in hln11, can test multiple
models while maintaining desirable statistical properties.

In Monte Carlo simulations, we show the empirical relevance of our results.
First, simulations indicate that not using excluded instruments may lead to
incorrect results. Second, we show that all four tests have good properties
without misspecification. Finally, we show that RV is able to conclude in
favor of the correct model in a misspecified setting with low bias, whereas
the other three testing procedures increasingly reject both models of conduct
as the sample size gets larger.

This paper discusses tools relevant to a broad literature seeking to
understand firm conduct in the context of structural models of demand and
supply. Investigating collusion is a prominent application (e.g. p83, s85,
b87, s92, glv92, gm98, n01, cw14, mw17, msw19, bd19, s20, fs20, es19). Other
important applications include common ownership (Kennedy, O’Brien, Song, and
Waehrer (2017), bcs20), vertical conduct (e.g. v07, bd10, Bonnet, Dubois,
Villas-Boas, and Klapper (2013), g13), price discrimination (ddf19), price
versus quantity setting (fl95), post-merger internalization (mw18), and non-
profit behavior (dmr20).

Many of the above examples involve contexts where the researcher does not
observe marginal cost. However, there are some important exceptions: in n01
for instance, accounting data on marginal costs are available. Other cases
include b15, is19, and Crawford, Lee, Whinston, and Yurukoglu (2019). Such
data are very helpful to assess firm conduct. While we discuss this case in
Section 3, we are mainly concerned with the more common case where this data
is not available to the researcher.

This paper is also related to econometric work on testing of non-nested
hypotheses. Important surveys of this area include gm94 and pw01. The AR
approach is developed originally in ar49 and is a central tool in the
literature on inference in the presence of weak instruments (for a recent
survey see ass19). The Cox approach was introduced by c61 and specialized to
GMM estimation in s92. v89 formulates a test of non-nested hypotheses for
models estimated with MLE, and rv02 extend the test to more general settings,
including GMM. hp11 further investigate the distribution of the rv02 test
statistic for the GMM case.111More recently, work has been done to improve the
asymptotic properties of the test. This includes s15 and sw17. We build on the
insights of the econometrics literature that performs inference in the
presence of model misspecification and highlights the importance of model
selection procedures when models are misspecified (w82; mp82; hi03; mo12).

The paper proceeds as follows. Section 2 describes the environment – a general
model of firm conduct. Section 3 discusses testing when true costs or markups
are observed, and introduces the concepts of model assessment and model
selection. Section 4 formalizes the conditions under which we can falsify a
model when true costs and markups are unobserved and introduces four
approaches to testing in this setting: EB, AR, Cox, and RV. In Section 5 we
establish properties of these testing procedures with no misspecification.
Section 6 examines the choice of moments and the choice of weights in
constructing the four test statistics. In Section 7, we turn attention to case
of misspecification and establish the properties of the four approaches in
this case. Section 8 discusses practical advice on testing conduct. Section 9
presents evidence from Monte Carlo simulations. In Section 10 we conclude.
Proofs to all propositions are found in Appendix A.

##  2 Model of Firm Conduct

We consider the problem of distinguishing between different types of firm
conduct in a market for differentiated products. For expositional simplicity,
we consider the case of two candidate models.222In Section 7.5 we discuss how
to perform testing for more than two models. We assume that we observe a set
of products $\mathcal{J}$ offered by firms across markets $t$. For
compactness, we use $i$ as a generic index for product $j$ in market $t$. We
observe price $\mathbf{p}_{i}$, market share $\mathbf{s}_{i}$, a vector of
product characteristics $\mathbf{x}_{i}$ that affects demand, and a vector of
observed cost shifters $\mathbf{w}_{i}$ that affects the product’s marginal
cost. For each variable $\mathbf{y}_{i}$, we denote as $\mathbf{y}$ the full
vector of $\mathbf{y}_{i}$ across the $n$ observations, and $\mathbf{y}_{t}$
as the subvector of values in market $t$. We assume that, for all markets $t$,
the demand system that generates elasticities is
$s_{t}=\mathbcal{s}(\mathbf{p}_{t},\mathbf{x}_{t},\bm{\xi}_{t})$, where
$\bm{\xi}_{t}$ is the vector of unobserved product characteristics. The
equilibrium in market $t$ is characterized by a system of first order
conditions arising from the firms’ profit maximization problems:

$\displaystyle\mathbf{p}=$
$\displaystyle\mathbf{\Delta^{*}_{0}}+\mathbf{c_{0}},\,\,\,$ (1)

where $\mathbf{\Delta^{*}_{0}}$ is the true vector of markup terms and
$\mathbf{c_{0}}$ is the true vector of marginal costs. Following the
literature, we assume that marginal costs are a linear function of observable
cost shifters w, so that
$\mathbf{c_{0}}=\textbf{w}\tau+\bm{\omega_{0}}$.333This assumption is not
necessary for our testing procedure to be valid. Further, this assumption is
not restrictive if a researcher constructs w flexibly from the data. For
instance, if a researcher observes variables $\bar{\textbf{w}}$ which shift
cost, w could be specified as $\textbf{W}(\bar{\textbf{w}})$ (e.g. W could be
a sieve expansion). We discuss the choice of w in Section
LABEL:sec:instruments

Cost shifters w are assumed to be exogenous throughout, so that
$E[\mathbf{w}_{i}\bm{\omega}_{0i}]=0$. Moreover, the coefficient $\tau$ is a
nuisance parameter, as it is not the primary object of interest in this
article where we focus on testing hypotheses on conduct. Hence, to streamline
notation, we find it convenient to define orthogonalized versions of the main
variables with respect to w. For each variable $\textbf{y},$ we denote its
orthogonalized version with respect to the vector of cost shifters w as
$y=M_{\textbf{w}}\textbf{y}$, where $M_{\textbf{w}}=I-P_{\textbf{w}}$ is the
residual maker matrix and
$P_{\textbf{w}}=\textbf{w}(\textbf{w}^{\prime}\textbf{w})^{-1}\textbf{w}^{\prime}$
is the projection matrix.444Throughout the paper we use projection matrices
and residual maker matrices, defined for a generic vector y as
$P_{\textbf{y}}=\textbf{y}(\textbf{y}^{\prime}\textbf{y})^{-1}\textbf{y}^{\prime}$
and $M_{\textbf{y}}=I-P_{\textbf{y}}.$ Thus a bolded variable $\mathbf{y}$ is
not orthogonalized while an unbolded variable $y$ is orthogonalized with
respect to w.

The researcher can formulate alternative models of conduct $m$, estimate the
demand system, and obtain estimates of markups $\hat{\Delta}_{m}$ under each
model $m$. There is a large literature devoted to the estimation of
elasticities and markups. To make progress on testing assumptions on the
supply side, we abstract away from the estimation step and we treat
$\Delta_{mi}=plim_{n\rightarrow\infty}\hat{\Delta}_{mi}$ as data.555To speak
to the practical application of testing procedures, we describe in Appendix C
how to adjust standard errors to allow for two-step estimation, and also
present Monte Carlo evidence where demand is estimated in a first step.
Further, in Section 7.1, we discuss the implications for testing of estimating
demand with and without the supply moments. Irrespective of the specific
functional form of markups $\Delta_{mt}$, in oligopoly models this markup term
is generally a function of both prices $p_{t}$ and market shares $s_{t}$.
Hence (1), for an assumed model $m$, becomes:

$\displaystyle p_{t}=\Delta_{mt}(p_{t},s_{t})+\omega_{mt}.$ (2)

Since our aim is to use the model and the data to test two non-nested models
of conduct, we can rewrite equation (2) as:

$\displaystyle p=$ $\displaystyle[\Delta_{1},\Delta_{2}]\theta+\omega$ (3)
$\displaystyle=$ $\displaystyle\Delta\theta+\omega$ (4)

where $\Delta$ is a $n$ by two vector, and $\theta$ is a two by one vector. In
the spirit of a70, Equation (3) constructs an artificial nesting model and the
two models correspond to different values of the parameter $\theta$:

$\displaystyle m=1:\theta=[1,0]^{\prime}\qquad vs\qquad
m=2:\theta=[0,1]^{\prime}.$ (5)

This nesting specification is general, and depending on the choice of $\Delta$
allows us to test many hypotheses on conduct found in the literature.
Canonical examples of such hypotheses include the nature of vertical
relationships, whether firms compete in prices or quantities, collusion,
intra-firm internalization, common ownership and nonprofit conduct.666In some
empirical settings the two models can be expressed as a nonlinear function of
parameters $\kappa$, so that estimating equation is instead:  $\displaystyle
p=\Delta(\kappa)+\omega,$ (6) and each model $m$ corresponds to a value
$\kappa_{m}$. Our formulation of the estimating equation encompasses the
comparison of any two models of conduct where $\Delta_{m}=\Delta(\kappa_{m})$.

We assume that the true vector of markups $\Delta^{*}_{0}$ can be written as

$\displaystyle\Delta^{*}_{0}=\Delta^{*}\theta_{0},$ (7)

so that the parameter $\theta_{0}$ selects the markups for true model of
conduct, and $\Delta^{*}$ contains well specified markups corresponding to the
two candidate models. Without loss of generality, we assume throughout the
article that $\theta_{0}=[1,0]^{\prime}$, so that model 1 is the true model of
conduct. It is possible that the vector of markups $\Delta$ observed by the
researcher differs from the vector $\Delta^{*}$. For example, one could
estimate elasticities with a misspecified model of demand. Depending on the
nature of the misspecification of markups implied by the two candidate models,
different testing environments are possible. We consider in the paper three
testing environments:

  * TE1

No Misspecification -  We assume that model 1 is the true model and markups
are not misspecified, so that $\Delta=\Delta^{*}$

  * TE2

Markup Misspecification -  We assume that model 1 is the true model but
markups are misspecified, so that $\Delta\neq\Delta^{*}$

  * TE3

Model Misspecification -  We assume that neither of the two models 1 and 2 is
the true model

To illustrate the difference between the three testing environments, consider
the case of testing Bertrand competition versus joint profit maximization. In
TE1, Bertrand may be the true model and markups are measured without error for
both Bertrand and joint profit maximization. In TE2, demand elasticities are
mismeasured so that the markups implied by Bertrand and joint profit
maximization are misspecified. In TE3, the true model is Cournot, so that
neither of the two models specified by the researcher is true.

Another important consideration for testing conduct is whether markups for the
true model $\Delta^{*}_{0}$ are observed. We consider first in Section 3 the
case where true markups are observed. We discuss instead the case where
$\Delta^{*}_{0}$ is unobserved in Sections 4 to 7 of the paper. In this case,
estimating or testing hypotheses based on Equation (2) requires instruments
for $\Delta_{mt}$, as markups are generally correlated with $\omega_{mt}$.
Note that this comes from two channels: one is direct, since $\Delta_{mt}$ is
a function of $p_{t}$, which is an explicit function of $\omega_{mt}$. The
other is due to the fact that $\Delta_{mt}$ is a function of shares $s_{t}$,
which in turn depend on the unobservable $\xi_{t}$, which may be correlated
with $\omega_{mt}$. b82 and bh14 provide intuition on what variation permits
the researcher to distinguish two modes of conduct, namely variation that
shifts and rotates the demand curve. Common choices of instrumental variables
of this type include the BLP instruments and the gh19 instruments. In recent
work, bcs20 explore the optimal instruments for testing. We do not specify
what the instruments are. Instead, we maintain that the researcher observes
exogenous variables $\bar{z}$ in the data and constructs the instruments as
$z=Z(\bar{z})$, such that the following assumption holds:777We discuss the
construction of $z$ from $\bar{z}$ in greater depth in Section
LABEL:sec:instruments

######  Assumption 1.

We assume that $z_{i}$ is a vector of $d_{z}$ excluded instruments for
$\Delta^{*}$, or $E[z_{i}\omega_{0i}]=0.$

This assumption provides a moment condition that can be used to test
hypotheses on $\theta$. Specifically, for any value of $\theta$, we construct
a sample moment function using the excluded instruments $z$ as:

$\displaystyle g(\theta)$
$\displaystyle=\frac{1}{n}z^{\prime}(p-\Delta\theta),$ (8)
$\displaystyle=\frac{1}{n}z^{\prime}\omega(\theta),$ (9)

so that, for each model $m$, the moment function takes the value
$g_{m}=g(\theta_{m})$.

Given the instruments $z$, we introduce the first stage projection coefficient

$\displaystyle\Gamma$
$\displaystyle=E[z_{i}z_{i}^{\prime}]^{-1}E[z_{i}\Delta_{i}^{\prime}]$ (10)
$\displaystyle=A_{zz}^{-1}A_{z\Delta},$ (11)

so that we define the projection of markups for model $m$ on $z$ as:

$\displaystyle\tilde{\Delta}_{m}=z\Gamma\theta_{m},$ (12)

which we refer to as predicted markups.

Finally, the following assumption summarizes regularity conditions that we
maintain throughout:

######  Assumption 2.

Assume that:

  * •

The data $(p_{i},\Delta_{i},\Delta^{*}_{i},z_{i}),i=1,2,...$ are jointly iid;

  * •

The random variables $p,z,\Delta$ and $\Delta^{*}$ have finite fourth moments;

  * •

The matrices $A_{\Delta\Delta}=E[\Delta_{i}\Delta_{i}^{\prime}]$,
$A_{\Delta^{*}\Delta^{*}}=E[\Delta^{*}_{i}\Delta^{*\prime}_{i}]$,
$A_{zz}=E[z_{i}z_{i}^{\prime}]$ and $E[\omega_{0}\omega_{0}^{\prime}\mid
z]=\Omega$ are positive semidefinite.

These assumptions are necessary for GMM and OLS estimators of the parameter
$\theta$ to be well defined, and help to derive the limiting distributions of
the test statistics we discuss in Section 4.

##  3 Nevo’s Menu Approach and Hypothesis Formulation

We consider in this section the ideal testing environment in which the
researcher observes not only markups implied by the two candidate models
$\Delta=\Delta^{*}$, but also the true markups (or equivalently marginal
costs) $\Delta^{*}_{0}$. For instance, accounting data may be available as in
n01.888In practice, n01 observes a noisy measure of $\Delta^{*}_{0}$. As a
benchmark, we abstract from measurement error in the markup data. If the
testing environment is TE1, the researcher can proceed by comparing directly
the markups $\Delta_{m}$ implied by each model $m$ with the data
$\Delta^{*}_{0}$. In fact, the researcher would only have to do this for one
observation.

Suppose instead that the researcher observes the distribution of
$\Delta^{*}_{0}$. Testing can be done by constructing a measure of lack of fit
between the true distribution of markups and the distribution of markups
implied by each model $m$. Denote the lack of fit in the population as
$\mathcal{F}_{m}$. For example, $\mathcal{F}_{m}$ could be the difference
between the median values of $\Delta_{m}$ and $\Delta^{*}_{0}$, or between
quantiles of the distributions of $\Delta_{m}$ and $\Delta^{*}_{0}$ as in n01.
One could also construct measures that compare the whole distributions such as
Kolmogorov-Smirnov statistics, or the (squared) distance between markups
$E[(\Delta^{*}_{0i}-\Delta_{mi})^{2}]$.

In order to evaluate models based on lack of fit $\mathcal{F}_{m}$, the
researcher may proceed in one of two directions: model assessment or model
selection.999See e.g. pw01 for a general discussion of these two strategies.
Model assessment concerns pitting a model $m$ against a set of alternatives,
and determining whether there is enough information in the data to reject that
model. Instead, model selection adopts a perspective where both models are
treated symmetrically, and the model which better fits the data asymptotically
is selected.

These two strategies result in a different formulation of null and alternative
hypotheses. The model assessment approach specifies for each model $m$ a null
hypothesis:

$\displaystyle H_{0,m}:\,\,\mathcal{F}_{m}=0$ (13)

versus an alternative of the form:

$\displaystyle H_{A,m}:\,\,\mathcal{F}_{m}\neq 0.$ (14)

By considering each model as a separate null hypothesis, this procedure relies
on an absolute, as opposed to relative, assessment of each model. Hence,
depending on the distances between the true markups and the implied markups
for each model, four cases may arise. Either both nulls are rejected, only one
is rejected, or neither is rejected. The researcher can conclude in favor of
one model only when one null is rejected and the other null is not rejected.
The failure to reject both nulls is not very informative, and may indicate
that both models imply similar markups (see also the discussion in gm94). The
rejection of both null hypotheses indicates misspecification, but gives no
indications to the researcher on how to proceed.

Instead, we can construct a model selection procedure by formulating a null of
the form:

$\displaystyle H_{0}:\,\,\mathcal{F}_{1}=\mathcal{F}_{2}$ (15)

Relative to this null, we can define two alternative hypotheses corresponding
to cases of asymptotically better fit of one of the two models:

$\displaystyle
H_{A,1}:\,\,\mathcal{F}_{1}<\mathcal{F}_{2}\qquad\text{and}\qquad
H_{A,2}:\,\,\mathcal{F}_{1}>\mathcal{F}_{2}$ (16)

A model $m$ is thus selected by this procedure if the null is rejected in
favor of the alternative that corresponds to better asymptotic fit of model
$m$. Intuitively, as long as the two models $m=1,2$ are asymptotically
different, this procedure will select the one that generates markups that are
closer to the true markups. So, whereas model assessment separately considers
the absolute fit of each model, model selection considers the relative fit of
the two models.

Hypothesis formulation thus interacts in an important way with the testing
environments described above. In TE1, where markups are well-specified, direct
comparison of the observed $\Delta^{*}_{0}$ and markups $\Delta^{*}_{m}$
implied by model $m$ allows a researcher to directly falsify $m$. In
environments TE2 and TE3, where markups and or the two hypotheses on conduct
are misspecified, a model assessment approach will lead to the asymptotic
rejection of both candidate models. Conversely, a model selection approach may
allow the researcher to select the model that is closer to the truth, thus
choosing asymptotically the true model as long as misspecification is not too
severe. We explore more in depth the interaction between hypothesis
formulation and misspecification in the common setup where the true markups
are not observed, which we discuss in the next sections of the paper.

##  4 Testing Without Cost Data

We noted in the section above that one can perform testing in environment TE1
by simply comparing $\Delta^{*}_{0}$ with the markups implied by the two
models when $\Delta^{*}_{0}$ are observed. Assuming no misspecification, this
comparison would permit the researcher to determine the correct model.

In contrast, we assume in this section that we do not observe true markups,
but we observe valid instruments that shift and rotate the demand curve. To
build intuition, we continue to maintain environment $TE1$ where markups for
both models are correctly specified and model 1 is the true model.101010In
later sections, we relax the conditions defined here for environments TE2 and
TE3

The canonical argument for distinguishing two models of conduct with this
source of variation is laid out in Figure 2 of b82, which illustrates how to
distinguish the hypothesis of perfect competition from the one of monopoly.
Suppose that we observe a market equilibrium
$\mathcal{E}_{t^{\prime}}=(\mathbf{p}_{t^{\prime}},\mathbf{q}_{t^{\prime}})$
in period $t^{\prime}$. With knowledge of the demand system, we can back out
markups $\mathbf{\Delta}_{t^{\prime}}$ corresponding to the two models of
conduct, which imply corresponding marginal costs
$(\mathbf{c}_{1t^{\prime}},\mathbf{c}_{2t^{\prime}}).$ Suppose that, in moving
from period $t^{\prime}$ to period $t$, demand has rotated or
shifted111111When marginal costs are constant, shifts of demand are sufficient
for identification. while cost hasn’t changed. Here we observe a new
equilibrium $\mathcal{E}_{t}$. Since cost did not change, we can use the costs
$(\mathbf{c}_{1t^{\prime}},\mathbf{c}_{2t^{\prime}})$ to calculate the prices
$(\mathbf{\tilde{p}}_{1t},\mathbf{\tilde{p}}_{2t})$ in the new equilibrium
predicted by the two models. We cannot falsify the model $m$ for which
$\mathbf{p}_{t}=\mathbf{\tilde{p}}_{mt}.$

While keeping costs fixed across different observations and markets may be
theoretically possible, it does not correspond to what we observe in most
empirical environments. In particular, costs depend on realizations of an
unobservable $\omega,$ which vary across products and markets. Thus, we
illustrate in Figure 1 the intuition behind testability of conduct. To do so,
we extend Figure 2 in b82 to our environment.

In Figure 1, we orthogonalize all variables with respect to w \- essentially
keeping the observable part of marginal cost fixed across markets. For a large
set of markets indexed by $t$, we observe the equilibrium $\mathcal{E}_{t}$,
for which $p_{t}=\Delta^{*}_{0t}+\omega_{0t}.$ However, we do not know the
nature of conduct: following b82 it could be monopoly, and the realized cost
shock would have been $\omega_{1t},$ or it could be perfect competition, and
the corresponding cost shock would have been $\omega_{2t}$. Across markets
$t$, $\mathcal{E}_{t}$ will vary for three reasons: movement in demand induced
by a vector of instruments $z$ that satisfy Assumption 1, a new draw of the
demand shock $\xi$, and a new draw of the cost shock $\omega_{0}$.

Figure 1: Testability of Conduct
Similar to b82, Figure 2, we illustrate how to test hypotheses on conduct
using instruments that shift and rotate the demand curve. In this case, model
1 corresponds to monopoly and model 2 corresponds to perfect competition.

In market $t$, we can use the demand system to solve for the implied markups
$\Delta_{mt}$ under each model. Given that we have orthogonalized all
variables with respect to w, $\tilde{p}_{mt}=\Delta_{mt}$ represents the
predicted price under model $m$. We can then compare the observed prices with
the prices predicted by each model. The predictions for both the true and the
wrong model will differ from the observed prices. For the true model, this
happens because of variation in the unobserved part of marginal cost
$\omega_{0t}$, which is uncorrelated with $z_{t}$. For the wrong model, there
is an additional source of difference between realized and predicted prices
arising from the different assumption on conduct. As the markups for each
model are correlated with $z_{t}$, their difference may also be correlated
with the instruments. This discussion provides a basis to falsify a model. We
assume, as the foundation to testing conduct, that the wrong model is
falsified:

######  Assumption 3.

The wrong model of conduct $m=2$ is falsified, so that:

$\displaystyle E[z_{i}(p_{i}-\Delta^{*}_{2i})]\neq 0.$ (17)

In TE1, $\Delta=\Delta^{*}$. Thus, given many markets, we cannot falsify a
model $m$ if $E[z_{i}(p_{i}-\Delta_{mi})]=0.$ Note that, given Equation (2),
this condition is equivalent to $E[z_{i}\omega_{mi}]=0$. Intuitively, this
reflects the fact that our benchmark for whether a model is true is that the
moment condition in Assumption 1 holds. This environment is a special case of
the nonparametric testing setup described in bh14.121212See their Section 6,
case (2). In fact, after conditioning on w, the marginal revenue function
implied by any model $m$ is $p_{i}-\Delta_{mi}$. So, under constant marginal
costs, their condition (28) for a model to not be falsified becomes:

$\displaystyle E[p_{i}-\Delta_{mi}\mid z_{i}]=0\qquad a.s.,$ (18)

which implies our condition above.

It useful to think about our ability to falsify models of conduct in terms of
predicted markups as defined in Equation (11). Consider the setting in TE1
where model 1 is the true model: Equation (16) implies model $2$ is
falsifiable if $E[z_{i}\Delta_{1i}]\neq E[z_{i}\Delta_{2i}]$. This condition
also ensures that the two models generally imply different vectors of
predicted markups such that $\tilde{\Delta}_{1}\neq\tilde{\Delta}_{2}$. This
provides a parallel to the setting discussed in Section 3. There, given that
true markups are observed, being able to falsify the incorrect model required
the level of markups to differ for the two models, or
$\Delta_{1}\neq\Delta_{2}$. When true markups are unobserved, falsifiability
of model 2 requires the level of markups predicted by the instruments to
differ, or $\tilde{\Delta}_{1}\neq\tilde{\Delta}_{2}$. The following lemma
summarizes this discussion and presents a condition under which testing models
is possible.

######  Lemma 1.

Suppose Assumption 1 holds, and let model $m=1$ be the true model. Any other
candidate model $m=2$ is falsified if and only if:

$\displaystyle E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{2i})^{2}]\neq 0.$ (19)

Thus, in TE1, condition (17) in Assumption 3 is equivalent to (19).

In light of the lemma, the ability to distinguish the two candidate models of
conduct fundamentally requires having at least one instrument that generates
different predicted markups for those models. For many pairs of hypotheses on
firm conduct explored in applications, the condition in Equation (19) is
typically satisfied. For instance, instruments always generate different
predicted markups when the two candidate models imply strictly ranked markups,
and for at least one of the two models the markups are a function of the
instruments so that $E[z_{i}\Delta_{mi}^{\prime}]>0$.131313In general, if
instruments are shifters and rotators of demand, markups for both models will
be functions of the instruments. An important exception is if one of the two
models is perfect competition, whereby markups are identically zero. In this
case the condition in the lemma is satisfied as long as for the alternative
model $m$ we have $E[z_{i}\Delta_{mi}^{*\prime}]>0.$

Although Lemma 1 provides a large sample condition under which testing is
possible, it does not immediately suggest a testing procedure. To test
alternative models of firm conduct in finite sample, we need to formulate
hypotheses and construct test statistics. We discuss in the rest of this
section the four main approaches taken in the literature. The first three: EB,
AR, and Cox, are designed to perform model assessment, while the fourth, RV,
adopts a model selection approach. Due to its popularity in the applied
literature, we start with an estimation based approach where testing is
conducted using Wald statistics.

###  4.1 Estimation Based Approach

Testing can be conducted as a by-product of estimation of the parameter
$\theta$. We refer to this procedure as estimation based, or EB. Recent
examples in the applied literature of estimation that lend themselves to this
testing procedure include cw14, mw17 and mw18. The estimating equation we
consider is

$\displaystyle p=$ $\displaystyle\Delta\theta+\omega,$ (20)

and for each model $m$ we define null and alternative hypotheses:

$\displaystyle H_{0}^{EB,m}:\theta=\theta_{m}\qquad vs\qquad
H_{A}^{EB,m}:\theta\neq\theta_{m},$ (21)

The test can be implemented with the Wald approach by checking whether each
model $m$ implies parameters that are close to the GMM estimates
$\hat{\theta}$.141414Alternatively, the test could be implemented with the
Likelihood Ratio approach by performing a J-test. As long as the GMM estimator
is constructed using the optimal weight matrix, these approaches are
equivalent. For ease of comparison with RV and AR, we focus our exposition on
the Wald approach. The corresponding test statistic is thus:

$\displaystyle T^{EB,m}$
$\displaystyle=(\hat{\theta}-\theta_{m})^{\prime}\hat{V}_{\hat{\theta}}^{-1}(\hat{\theta}-\theta_{m}),$
(22)

where $\hat{V}_{\hat{\theta}}$ is a consistent estimator of the variance of
$\hat{\theta}$.

Notice that the condition in Lemma 1, while sufficient for falsifying model 2,
is not sufficient for identification of the parameter $\theta$, which is
necessary for the EB procedure. When performing EB, we have then to maintain a
stronger assumption:

######  Assumption 4.1a.

The matrix $A_{\Delta^{*}z}=E[\Delta_{i}^{*}z_{i}^{\prime}]$ has rank equal to
two.

In particular, this full rank assumption requires that we have at least two
instruments in our setting.151515The three other procedures to be introduced
in Section 4.2-4.4, however, only require the condition in Lemma 1 to
distinguish a wrong model from the true model. Unlike EB, all three of them
could be implemented with only one instrument. This assumption implies the
condition in Lemma 1.

As common in the literature, we choose $\hat{\theta}$ to be the 2SLS estimator
in our implementation of the test. We further discuss the choice of weight
matrix in Section 6.2. Under the null hypothesis corresponding to model $m$,
the statistic $T^{EB,m}$ is distributed according to a $\chi^{2}_{2}$
distribution. Hence, comparing the value of $T^{EB,m}$ with the corresponding
critical value from $\chi^{2}_{2}$ yields a test with the correct size for the
null corresponding to the true model $m$.

###  4.2 Anderson-Rubin Approach

In this approach the researcher defines, for each of the two models $m$ an
equation:

$\displaystyle p-\Delta_{m}=z\pi_{m}+\eta_{m},$ (23)

and then performs the test of the null hypothesis that $\pi_{m}=0$ with a Wald
test.161616The test could be implemented as a t-test if $z$ is a scalar. The
F-test and t-test implementations correspond to the Likelihood Ratio approach
and Wald approach, respectively. This procedure is similar to an ar49 testing
procedure, which accommodates hypothesis testing of endogenous linear models
in the presence of weak instruments. For this reason, we refer to this
procedure as AR. A recent example of testing in this spirit is bd19. Formally,
for each model $m$, we define the null and alternative hypotheses:

$\displaystyle H_{0}^{AR,m}:\,\,\pi_{m}=0,\qquad vs\qquad
H_{A}^{AR,m}:\,\,\pi_{m}\neq 0.$ (24)

We define the test statistic of the AR test for model $m$ as:

$\displaystyle T^{AR,m}$
$\displaystyle=\hat{\pi}^{m\prime}\hat{V}_{\hat{\pi}_{m}}^{-1}\hat{\pi}_{m}$
(25)

where $\hat{\pi}_{m}$ is the OLS estimate of $\pi_{m}$ and
$\hat{V}_{\hat{\pi}_{m}}$ is a consistent estimator of the variance of
$\hat{\pi}_{m}$. If $\hat{V}_{\hat{\pi}_{m}}$ is the estimator under
homoskedasticity, we have:

$\displaystyle\hat{V}_{\hat{\pi}_{m}}=(z^{\prime}z)^{-1}\hat{\sigma}_{\eta_{m}},$
(26)

where $\hat{\sigma}^{2}_{\eta_{m}}$ is an estimator of the variance of
$\eta_{m}$. Thus our statistic takes on the form defined in ar49 and
ss97.171717Although we use the variance estimator under homoscedasticity for
analytical convenience in the derivations of this paper, it is easy to
implement the test with the standard heteroscedasticity-consistent estimators
of variance. Depending on the empirical context, the researcher may want to
choose other forms of the estimator $\hat{V}_{\hat{\pi}_{m}}$ that allow, for
instance, for clustered standard errors. Under the null hypothesis
corresponding to model $m$, the statistic $T^{AR,m}$ is distributed according
to a $\chi^{2}_{d_{z}}$ distribution. Hence, comparing the value of $T^{AR,m}$
with the corresponding critical value from $\chi^{2}_{d_{z}}$ yields a test
with the correct size for the null corresponding to the true model $m$.

###  4.3 Cox Approach

The next testing procedure we consider is inspired by the c61 approach to
testing non-nested hypotheses. v07 is a prominent example of an applied paper
that uses this testing procedure. To perform a Cox test, we formulate two
different pairs of null and alternative hypotheses for each model $m$, based
on the moment conditions $\mathcal{g}_{m}=\mathcal{g}(\theta_{m})$, the
population analogue of the sample moment conditions $g_{m}$ defined in
Equation (8). Specifically, for model $m$ we formulate:

$\displaystyle H_{0}^{Cox,m}:\mathcal{g}_{m}=0,\qquad vs\qquad
H_{A}^{Cox,m}:\mathcal{g}_{-m}=0,$ (27)

where $-m$ denotes the alternative to model $m$. To implement the Cox test in
our environment we follow Smith (1992). The test statistic we use for model
$m$ is:

$\displaystyle T^{Cox,m}$
$\displaystyle=\frac{\sqrt{n}}{\hat{\sigma}_{Cox}}\bigg{(}g_{-m}^{\prime}Wg_{-m}-g_{m}^{\prime}Wg_{m}-(g_{-m}-g_{m})^{\prime}W(g_{-m}-g_{m})\bigg{)},$
(28)

where $\hat{\sigma}_{Cox}^{2}$ is a consistent estimator of the asymptotic
variance of the numerator of $T^{Cox,m}$ and $W$ is a positive semidefinite
weight matrix. As shown in s92, this statistic is distributed according to a
standard normal distribution under the null hypothesis. The choices of moments
and weights are further discussed in Section 6.1 and 7.4 respectively.

###  4.4 Rivers-Vuong approach

A prominent approach to testing non-nested hypotheses, which can be applied to
testing firm conduct, is the one developed in v89 and then extended to models
defined by moment conditions in rv02. Recent examples of this test in the
applied literature are mvz13, bcs20, dmr20, and s20. Following rv02, the null
hypothesis for the test is that the two models $m=1,2$ are asymptotically
equivalent, or

$\displaystyle H_{0}^{RV}:\,\,\mathcal{Q}_{1}=\mathcal{Q}_{2},$ (29)

where $\mathcal{Q}_{m}$ is a measure of fit for model $m$ in the population.
Relative to this null, we can define two alternative hypotheses corresponding
to cases of asymptotically better fit of one of the two models:

$\displaystyle
H_{A}^{RV,1}:\,\,\mathcal{Q}_{1}<\mathcal{Q}_{2}\qquad\text{and}\qquad
H_{A}^{RV,2}:\,\,\mathcal{Q}_{1}>\mathcal{Q}_{2}$ (30)

Defining $Q_{m}$ as the sample analogue of $\mathcal{Q}_{m}$, the test
statistic is:

$T^{RV}=\frac{\sqrt{n}}{\hat{\sigma}_{RV}}(Q_{1}-Q_{2}),$ (31)

where $\hat{\sigma}^{2}_{RV}$ is a consistent estimator of the asymptotic
variance of the difference in the measures of fit. rv02 show that the
distribution of the test statistic $T^{RV}$ is standard normal under the
null.181818When $\sigma^{2}_{RV}=0$, the RV test statistic becomes degenerate,
a well documented issue in the econometrics literature. While we maintain
$\sigma^{2}_{RV}>0$, we return to this issue in Section 6.2.

In this paper we define lack of fit via the GMM objective function. Although
the test can be defined for more general environments, in our setting we need
to account for endogeneity, making GMM an appropriate choice. Given the sample
moments defined in (8):

$\displaystyle Q_{m}$ $\displaystyle=g_{m}^{\prime}Wg_{m}$ (32)

where $W$ is a positive semi-definite weight matrix. We describe the choice of
moments and weights in greater detail in Section 6.1 and 7.4 respectively.

Having described the four testing procedures we consider in the article, we
develop a comparison of their properties in the next section.

##  5 Comparison among the tests

In this section, we explore the statistical properties of the four testing
procedures defined above. To fix ideas, we first explore the stylized
environment of TE1 in which there is no misspecification. Then we turn
attention to the more relevant environments of TE2 and TE3 where models are
misspecified.

###  5.1 Testing without misspecification

Suppose that the researcher faces a testing environment of the type TE1 where
true markups $\Delta^{*}_{0}$ are not observed, but well-specified markups
$\Delta=\Delta^{*}$ are available. Suppose moreover that there exists a valid
set of instruments as stated in Assumption 1, and that we use such instruments
to form moments $g(\theta)$ as defined in Equation (8). As is well known, all
four testing procedures defined in Section 4 - namely, EB, AR, Cox, and RV -
have the correct size under these conditions.

In this section, we seek to gain further insight into the properties of these
tests by characterizing the regions where the null is satisfied, and the
regions where the null is not satisfied and the tests are consistent. To
facilitate this characterization, we introduce the assumption of homoskedastic
errors:

######  Assumption 5.

Assume that the error term $\omega_{0i}$ is iid, so that
$E[\omega_{0i}^{2}|z]=\sigma_{\omega_{0}}^{2}$.

For the RV and Cox testing procedures, which rely on GMM objective functions,
we form the test statistics using the weight matrix $W=A_{zz}^{-1}$, as it is
efficient under Assumption 5. We can then prove the following proposition:

######  Proposition 1.

Suppose that the testing environment is TE1, the true markups are unobserved,
and that Assumptions 1, 2, 4.1a and 5 are satisfied. Then we can derive, for
each test statistic, the following convergence in probability results:

(i) $\displaystyle\frac{T^{EB,m}}{n}$
$\displaystyle\rightarrow_{p}\frac{E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{mi})^{2}]}{\sigma^{2}_{\omega_{0}}}$
(ii) $\displaystyle\frac{T^{AR,m}}{n}$
$\displaystyle\rightarrow_{p}\frac{E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{mi})^{2}]}{\sigma^{2}_{\eta_{m}}}$
(iii) $\displaystyle\frac{T^{Cox,m}}{\sqrt{n}}$
$\displaystyle\rightarrow_{p}\frac{2E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{mi})(\tilde{\Delta}_{-mi}-\tilde{\Delta}_{mi})]}{\sigma_{Cox}}$
(iv) $\displaystyle\frac{T^{RV\,\,\,}}{\sqrt{n}}$
$\displaystyle\rightarrow_{p}\frac{-E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{2i})^{2}]}{\sigma_{RV}}.$

We explore the implications of this proposition in a corollary.

######  Corollary 1.

Suppose the testing environment is TE1 and satisfies the assumptions of
Proposition (1). Then:

  1. 1.

The null hypothesis for EB, AR, and Cox are satisfied for model $m=2$, and the
null hypothesis of RV is satisfied if:

$\displaystyle E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{2i})^{2}]=0$

  2. 2.

If instead $E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{2i})^{2}]\neq 0$ all the
tests are consistent.

The corollary illustrates that for all four testing procedures directly
implement the falsifiability condition in Lemma (1). If model 2 yields the
same predicted markups as the true model 1, the moment conditions for model 2
are satisfied asymptotically. For the model assessment procedures, the null
that model 2 is true is satisfied, and for RV the null that model 2 fits as
well as model 1 is satisfied. Conversely, when the instruments generate
different predicted markups for the two models, the condition in Lemma (1)
holds. In this case the moment condition is violated for model 2 and
asymptotically this model will be rejected by all four testing procedures with
probability one. Although the testing procedures that we consider differ, they
all share the fundamental feature of being able to distinguish different
models of conduct insofar as these models imply different predicted markups.
Thus, in environment TE1, statistical power depends on the condition in Lemma
1 being satisfied, which requires having excluded instruments.

While the four tests all reject the wrong model asymptotially in TE1 as long
as the falsefiability condition holds, they may have different performance in
finite sample. In particular, we can show, using local alternatives, that a
strict ranking in power exists for the three model assessment procedures. In
particular, Cox is the most powerful test while EB is weakly more powerful
than AR. AR has particularly low power when the number instruments is large.
In the stylized setting of TE1 (and only in this setting), it is not possible
to perform local power analysis for RV. We return to this point in Section
6.2.

Important differences in the performance of these tests arise when we consider
the possibility of misspecification. In practice, a researcher might find
herself in environment TE2 where markups are misspecified due to either demand
or cost. Or the both models could themselves be misspecified in environment
TE3. In the next three subsections, we discuss, in turn, the relative
performance of the testing procedures when demand, cost, or the models are
misspecified.

###  5.2 Testing with demand misspecification

We maintain here environment TE2, in which one of the two models of conduct we
are considering is correct, but we allow markups to be misspecified through
demand elasticities. In theory, demand systems could be estimated
nonparametrically (e.g. c20), but data limitations or computational
constraints currently preclude these approaches in most applications. Hence,
researchers rely on parametric estimates of demand elasticities. While these
can be very good approximations of reality, some misspecification is likely
and can have implications for the testing procedures we describe.

In particular, demand misspecification introduces bias into our testing
environment, and interesting differences arise in the relative performance of
the procedures we consider. To formally discuss this kind of misspecification,
we will distinguish between the true matrix of markups $\Delta^{*}$, and the
misspecified matrix of markups $\Delta$ which the researcher has available. To
discuss testing in environment TE2 we introduce a modification of Assumption
4.1a:

######  Assumption 4.1b.

The matrix $A_{\Delta z}=E[\Delta_{i}z_{i}^{\prime}]$ has rank equal to two.

This assumption allows us to compute the EB test statistic with misspecified
markups, and implies that the two models under consideration are testable even
in an environment where markups are misspecified. To quantify the effect of
misspecification, we define bias as the mean squared error in predicted
markups under the true model of conduct:

$\displaystyle B=E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{0i})^{2}].$ (33)

[CHANGE THE WORDING, INSTEAD OF BIAS USE DEGREE OF MISSPECIFICATION OR
SOMETHING ALONG THESE LINES] As long as bias is positive, it will be
consequential for testing. Moreover, bias is most severe when it makes an
incorrect model of firm conduct seem closer to the truth than the correct
model of conduct. The two parts of the following assumption ensure that bias
is present, but not severe:

######  Assumption 6.

We assume that TE2 is a low bias environment and model $m=1$ is the true model
of conduct, so that $B=E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{1i})^{2}]$,
and:

  * (i)

$B>0$, and

  * (ii)

$B<E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{2i})^{2}]$.

Given the state of literature on demand estimation, and the increasing
availability of more flexible and nonparametric methods, this assumption is
sensible in many applied environments. We can then prove the following
proposition:

######  Proposition 2.

Suppose that markups $\Delta^{*}$ are unobserved and that Assumptions 1, 2,
4.1a, 4.1b and 5 are satisfied. Then we can derive, for each test statistic,
the following approximate convergence in probability results:

(i) $\displaystyle\frac{T^{EB,m}}{n}$
$\displaystyle\rightarrow_{p}\frac{E[({\tilde{\Delta}}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]}{\sigma^{2}_{\omega_{0}}}$
(ii) $\displaystyle\frac{T^{AR,m}}{n}$
$\displaystyle\rightarrow_{p}\frac{E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]}{\sigma^{2}_{\omega_{0}}}$
(iii) $\displaystyle\frac{T^{Cox,m}}{\sqrt{n}}$
$\displaystyle\rightarrow_{p}\frac{E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{-mi})^{2}]-E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]-E[(\tilde{\Delta}^{*}_{mi}-\tilde{\Delta}_{-mi})^{2}]}{2\sigma_{\omega_{0}}\sqrt{E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{2i})^{2}]}}$
(iv) $\displaystyle\frac{T^{RV\,\,\,}}{\sqrt{n}}$
$\displaystyle\rightarrow_{p}\frac{E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{1i})^{2}]-E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{2i}))^{2}]}{2\sigma_{\omega_{0}}\sqrt{E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{2i})^{2}]}}.$

The results in Proposition 3 have stark consequences on the asymptotic
behavior of the testing procedures, which we highlight in the following
corollary:

######  Corollary 2.

Suppose that the testing environment is TE2 and satisfies the assumptions of
Proposition 3. Then:

  1. 1.

Under Assumption 6(i), RV rejects the null of equal fit, and the EB, AR and
Cox testing procedures reject the null for $m=1$ corresponding to the true
model with probability that goes to one as the sample size increases;

  2. 2.

Under Assumptions 6(i) and (ii), RV rejects the null of equal fit in favor of
the alternative corresponding to the true model with probability that goes to
one as the sample size increases.

Corollary 2 highlights an important difference between RV and the other
testing procedures. When markups are misspecified, EB, AR, and Cox (the model
assessment procedures) reject the null corresponding to the correct model of
conduct with probability that goes to one. Instead, RV (the model selection
procedure) will reject the null of equal fit in favor of the true model as
long as the misspecification is not too severe. In particular, RV will reject
in favor of the true model $m=1$ so long as it is closer to the truth in the
sense of Assumption 6.

Note that Assumption 6 holds if and only if

$\displaystyle
E[(\tilde{\Delta}_{0i}-\tilde{\Delta}_{2i})^{2}]>-2E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{0i})(\tilde{\Delta}_{0i}-\tilde{\Delta}_{2i})].$
(34)

Intuitively, unless there is a sufficiently strong negative covariance between
differences in predicted markups due to misspecification, and differences in
predicted markups due to the wrong model of conduct, RV will reject in favor
of the true model.

Figure 2: Effect of Bias on Testing Procedures This figure illustrates how
bias determines asymptotic outcomes of the RV test (in panel A) and of the AR,
Cox and EB tests (in panel B).

Figure 2 represents the results of Corollary 2. The space with coordinates
$E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]$ for $m=1,2$ is a
characterization of all possible asymptotic testing environments. In panel A
we see that RV asymptotically rejects in favor of the true model 1 as long as
the black dot - which represents the realization of the testing environment in
the data - lies to the left of the 45-degree line, in the low bias region. In
panel B we see instead that any departure from the vertical axis (which
represents TE1) results in a rejection of both models.

To discuss more formally the behavior of the testing procedures we analyze
under misspecification of markups, we consider the limiting distribution of
the test statistics under a true null in a local alternatives setting. This
restriction serves as a tool to approximate the finite sample power of each
test in an environment where the two models are hard to tell apart. The two
forces at play here, which determine the probability of rejecting the null,
are bias due to misspecification, and noise. We already defined bias as the
term $B$, the mean squared error of markups corresponding to the true model.
In general, we think of noise as determined by both $\sigma^{2}_{\omega_{0}},$
which captures the degree to which pricing is driven by random cost shocks,
and the sample size $n$. Proposition 3 describes the probability limit of the
test statistics as sample size gets larger, reducing noise. In the local
alternatives environment the increase in precision due to larger samples is
offset by the models getting closer to each other, thus shutting down sample
size as a source of noise and allowing us to focus on the role of
$\sigma^{2}_{\omega_{0}}$.

In the context of TE2, we specify local alternatives assumptions for model
assessment and model selection procedures separately. We do so because we need
to converge to the null space for each procedure at an appropriate rate, and
model assessment and model selection procedures have different nulls. Local
alternatives are defined in the following assumption:

######  Assumption 7.

Assume that the models we consider represent local alternatives.

  * •

For the model assessment procedures EB, AR and Cox, assume
$\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{m}=\frac{\rho^{*}}{\sqrt{n}}+o_{p}(n^{-1/2})$,
where $\rho^{*}$ is a finite vector, for $m=1,2$. Moreover
$\hat{\Gamma}^{*}_{0}=\Gamma^{*}_{0}+o_{p}(1),\hat{\Gamma}_{m}=\Gamma^{*}_{0}+o_{p}(1)$
for a nonzero vector $\Gamma^{*}_{0}$ and $m=1,2$.

  * •

For RV, assume
$\hat{\Gamma}_{1}+\hat{\Gamma}_{2}-2\hat{\Gamma}^{*}_{0}=\frac{c}{\sqrt{n}}+o_{p}(n^{-1/2})$
for a nonzero vector $c$. Further suppose that
$\hat{\Gamma}_{1}-\hat{\Gamma}_{2}=d+o_{p}(1)$ for a nonzero vector $d$.

We can thus establish the following:

######  Proposition 3.

Assume that the testing environment is TE2, that true markups are unobserved,
and that assumptions 1, 2, 4.1a, 5, and 7 are satisfied. We also assume that
the true parameter is $\theta_{0}=\theta_{1}$ and the null hypothesis for AR,
EB and Cox is model $m=1$. Then we can derive, for each test statistic, the
following convergence in distribution results:

(i) $\displaystyle T^{EB,1}$
$\displaystyle\rightarrow_{d}\chi^{2}_{2}\bigg{(}\frac{B^{\prime(n)}}{\sigma^{2}_{\omega_{0}}}\bigg{)}$
(ii) $\displaystyle T^{AR,1}$ $\displaystyle\rightarrow_{d}\
\chi^{2}_{d_{z}}\bigg{(}\frac{B^{(n)}}{\sigma^{2}_{\omega_{0}}}\bigg{)}$ (iii)
$\displaystyle(T^{Cox,1})^{2}$
$\displaystyle\rightarrow_{d}\chi^{2}_{1}\bigg{(}\frac{(B^{(n)})^{2}}{4\sigma^{2}_{\omega_{0}}E[(\tilde{\Delta}^{(n)}_{1i}-\tilde{\Delta}^{(n)}_{2i})^{2}}\bigg{)}$
(iv) $\displaystyle(T^{RV})^{2}$
$\displaystyle\rightarrow_{d}\chi^{2}_{1}\bigg{(}\frac{(B^{(n)}-E[(\tilde{\Delta}^{*(n)}_{0i}-\tilde{\Delta}^{(n)}_{2i})^{2}])^{2}}{4\sigma^{2}_{\omega_{0}}E[(\tilde{\Delta}^{(n)}_{1i}-\tilde{\Delta}^{(n)}_{2i})^{2}]}\bigg{)}$

where we define the modified bias constant:

$\displaystyle
B^{\prime}=E[(\tilde{\tilde{\Delta}}^{*}_{0i}-\tilde{\Delta}_{0i})^{2}],$

and all predicted markups and bias terms are computed using the stable
$\tilde{\Delta}^{(n)}$.

The proposition shows that, under misspecification, the test statistics have
noncentral $\chi^{2}$ distributions whose noncentrality depends on bias and
noise. For EB, AR and Cox, the noncentrality, and hence the probability of
rejecting the true model of conduct, is proportional to bias (as measured by
the stable versions of $B$ and $B^{\prime}$) and inversely proportional to
noise (as measured by $\sigma^{2}_{\omega_{0}}$). Practically, this implies
that - when there is little noise in the testing environment - these
procedures will reject true models of conduct even when the bias due to
misspecification of markups is very small. While Proposition 3 shows that, in
large samples, the null is rejected with probability that approaches one,
Proposition 4 shows that, in finite samples, rejecting the null for these
procedures depends on the relationship between bias and noise. Importantly,
EB, AR, and Cox only fail to reject the true model of conduct when the noise
is sufficiently large.

The RV test, on the other hand, behaves differently. The noncentrality, and
thus the probability of rejecting the null of equal fit, depends on the
quantity:

$\displaystyle
B^{(n)}-E[(\tilde{\Delta}^{*(n)}_{0i}-\tilde{\Delta}^{(n)}_{2i})^{2}],$ (35)

the difference between two objects: the bias and a term equal to the distance
between the predicted markups of the true model without misspecification and
the predicted markups of the incorrect model $m=2$ with misspecification. As
long as the lack of fit of the incorrect model is larger than bias $B$ as
implied by Assumption 6, the RV test may reject the null in favor of the true
model. Whether it does so depends again on noise. Crucially though, and unlike
EB, AR, and Cox, less noise results in a higher probability of rejecting in
favor of the true model for any given level of the difference in (35).

These points are illustrated in Figure 3. Each panel represents, for either
the model selection or model assessment approach, and for either a high or low
noise environment, the outcome of testing in the space with coordinates
$E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]$ for $m=1,2$. Blue
regions with horizontal lines indicate concluding in favor of the model 1,
while regions with vertical red shading indicate concluding in favor of model
2. The two panel on the left show that, as noise decreases, RV becomes more
conclusive, since the shaded regions expand. Conversely, as noise decreases
the model assessment procedures tend to reject both models more often, as the
shaded regions approach the two axes. For example, consider one realization of
the data represented by the black dot. As it represents a low-bias
environment, RV rejects the null and concludes in favor of model 1 as long as
the noise is low. Model assessment procedures, instead, only conclude in favor
of model 1 in a high noise environment, and reject both models if the noise is
low.

Figure 3: Effect of Noise on Testing Procedures This figure illustrates how
noise affects asymptotic outcomes of the RV test (in panels A and C) and of
the AR, Cox and EB tests (in panels B and D).

What drives the distinction between EB, AR and Cox on one side, and RV on the
other, is how they formulate the null hypothesis. In turn, this difference is
linked to the two fundamental goals of model assessment and model selection.
When adopting a model assessment approach, we devise procedures that use the
data to falsify models of conduct: this is what EB, AR and Cox test are
designed to do. Crucially, any evidence that the predicted markups diverge
from the true predicted markups will lead to rejection asymptotically. This is
entirely appropriate when a researcher wants to learn whether a model
generates correct predicted markups. However in the presence of
misspecification, likely to be pervasive in practice, this approach has
limitations. When the data become more informative, all models (even very
close to be correct) will be rejected. Conversely, not rejecting the null
often indicates that the data are not informative enough, rather than that the
model is correct.

Alternatively, a researcher may pursue a model selection angle. By being open
to the possibility of misspecification, we can learn which models of conduct
better fits the data. This is what is accomplished with an RV procedure. In
the model selection logic, pairwise comparisons between hypotheses are carried
out examining their relative fit. As an analogy, model selection compares the
relative fit of two candidate models and asks whether a “preponderance of the
evidence” suggest that one model fits better than the other. Meanwhile, model
assessment (and hence AR, EB, and Cox) uses a higher standard of evidence,
asking whether a model is not falsifiable “beyond any reasonable doubt.” While
we may want to be able to conclude in favor of a model of conduct beyond any
reasonable doubt, this is not a realistic goal in the presence of
misspecification. However, if we lower the evidentiary standard, we can still
make progress and learn about the true nature of firm conduct.

###  5.3 Testing with misspecification of Marginal Cost

Above, we discussed the implications of demand misspecification on the testing
procedures. Now, we turn our attention to the misspecification of marginal
cost. Suppose:

$\mathbf{p}=\mathbf{\Delta}^{*}_{0}+\mathbf{w}\tau+\bm{\omega_{0}}$

is the DGP so that $E\left(\mathbf{\omega_{0}}|\mathbf{z,w}\right)=0$ and the
researcher observes $\Delta^{*}_{0}$. However, the researcher uses
misspecified cost-shifters $\mathbf{w_{a}}$ for testing conduct. The
difference in $\mathbf{w}$ and $\mathbf{w_{a}}$ may be due to functional form
or the omission/addition of relevant cost shifters. For each model $m$ we can
write:

$\displaystyle\mathbf{p}$
$\displaystyle=\left[\mathbf{\Delta}^{*}_{m}+\left(\mathbf{w}\tau-\mathbf{{w_{a}}}\tau_{\mathbf{a}}\right)\right]+\mathbf{{w}_{a}}\tau_{\mathbf{a}}+\bm{\omega}_{m}$
$\displaystyle={\mathbf{\Delta}^{C}_{m}}+\mathbf{{w_{a}}}\tau_{\mathbf{a}}+\bm{\omega}_{m}$
(36)

so that for any model $m$, including the true one, $\mathbf{\Delta}^{C}_{m}$
is different than $\mathbf{\Delta}^{*}_{m}$.

We assume that misspecification is consequential, but that the vector of cost
shifters $\mathbf{w_{a}}$ only includes variables that are orthogonal to the
original error term:

######  Assumption 8.

For the misspecified vector of cost shifters $\mathbf{w_{a}}$, the following
holds:

$\displaystyle E[\bm{\omega_{0}}\mid\mathbf{w_{a}},\mathbf{z}]$
$\displaystyle=0.$ (37)

This happens, for instance, if $\mathbf{w_{a}}$ is a subset of $\mathbf{w}$
and $\bm{\omega_{0}}$ is mean independent of
$(\textbf{w},\textbf{z})$.191919If Assumption 8 does not hold, the
misspecification of marginal cost is introducing an additional source of
endogeneity, which is not addressed by the instrument vector $z$. Under
Assumption 8, the exclusion restriction is satisfied for the true model of
conduct with the wrong marginal cost included if markups are given as
$\bm{\Delta}^{C}_{0}$ in Equation (36). This transformation of the DGP shows
that misspecification of costs can be turned into misspecification of markups.
Here though, when a researcher uses misspecified costs $\mathbf{w_{a}}$, it is
as if $\bm{\Delta}^{C}$ are the correctly specified unobserved markups, in the
sense that $\bm{\Delta}^{C}_{0}$ satisfies the moment condition. If demand is
correctly specified, a researcher will observe markups as $\bm{\Delta}^{*}$.
Now, $\bm{\Delta}^{*}_{0}$ fails to satisfy the moment condition given cost
shifters $\textbf{w}_{a}$. We formalize this discussion in a corollary to
Proposition 3:

######  Corollary 3.

Suppose that the testing environment is TE2, that demand is correctly
specified, and that $p,\Delta,$ and $z$ have been orthogonalized with respect
to $\textbf{w}_{a}\neq\textbf{w}$. Further suppose that Assumptions 1, 2,
4.1a, 4.1b, 5 and 8 are satisfied. Then:

  * •

The EB, AR, and Cox testing procedures reject the null for any $m$ with
probability that goes to one as the sample size increases;

  * •

RV rejects the null of equal fit in favor of the alternative $m$ which is
closer to the truth in the following sense:

$\displaystyle
E[(\tilde{\Delta}^{C}_{0i}-\tilde{\Delta}^{*}_{1i})^{2}]<E[(\tilde{\Delta}^{C}_{0i}-\tilde{\Delta}^{*}_{2i})^{2}].$

The corollary shows that the effects of cost misspecification can be fully
understood through the lens of markup misspecification. In turn,
misspecification of markups which violates the moment condition affects all
the testing procedures we have considered. While AR, EB, and Cox reject both
models if given enough data, RV will select the right model asymptotically if
the cost misspecification is not too severe. To address the possibility of
misspecification in cost or to reduce its severity, one may want to specify
the matrix $\mathbf{w}$ flexibly from the data. We return to this point in
Section LABEL:sec:instruments.

###  5.4 Testing with model misspecification

In this subsection we consider the testing environment TE3, where neither of
the two models is the true model and $\Delta^{*}_{0}$ is not observed. For
instance, suppose that the true model in the DGP is Cournot competition, but
the researcher decides to investigate whether firms compete a la Bertrand or
pursue joint profit maximization.

In this environment, testing the models of Bertrand and joint profit
maximization will not allow the researcher to learn the true mode of
competition. A model assessment approach, at best, can lead to a rejection of
both candidate models. However, if the ultimate goal is to learn which of the
two models under consideration best approximates the truth, a model selection
procedure can be useful. In particular, the researcher can still learn which
model generates predictions of markups that are more accurate.

More formally, we first introduce the following assumption:

######  Assumption 9.

For any model of conduct $m=1,2$, the following inequality holds:

$\displaystyle E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]\neq 0$
(38)

This assumption, parallel to the condition in Lemma 1, ensures that the
instruments allow the researcher to distinguish the markups associated with
model $m$ from the true markups. Given that neither model is correct in TE3,
Assumption 9 relaxes the ranking on
$E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{1i})^{2}]$ and
$E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{2i})^{2}]$ imposed in Assumption
6. With Assumption 9, we can state the following corollary to Proposition 2

######  Corollary 4.

Suppose that the testing environment is TE3, and that Assumptions 1, 2, 4.1a,
4.1b, 5 and 9 are satisfied. Then:

  * •

The EB, AR, and Cox testing procedures reject the null for any $m$ with
probability that goes to one as the sample size increases;

  * •

RV rejects the null of equal fit in favor of the alternative $m$ which is
closer to the truth in the following sense:

$\displaystyle
E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]<E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{-mi})^{2}].$

In the testing environment TE3, where neither of the vectors of markups
corresponding to the two candidate models is correct, the EB, AR, and Cox
procedures will always reject any candidate model as long as the data are
informative enough. Conversely, RV will point in the direction of the model
that appears closer to the truth in terms of predicted markups. However, this
relative assessment does not ensure that the chosen model $m$ is close to the
truth according to any absolute metric.

##  6 The Role of Instruments in Testing for Conduct

All tests described in Section 4, including RV, can be written as functions of
the moments defined in (8). These moments are constructed using valid,
excluded instruments $z$, so that the moment condition holds for the true
model. The existence of such instruments is crucial for testing conduct, as
the results in Section 5 crucially relied on a small set of valid and strong
instruments. In this section, we further formalize the impact on instruments
on testing, both asymptotically and in finite sample. We do so by providing
novel results on the performance of the RV test when these conditions for the
instruments are not satisfied.

First, we begin by illustrating the importance of forming moments $g_{m}$ with
excluded instruments. In particular, we show that, when measures of fit are
constructed without instruments, tests of conduct are misleading. This
discussion is motivated by prominent examples in the literature which do not
use excluded instruments to construct test statistics.

In many empirical settings, the standard instruments constructed from the
exogenous variation in the data may be weak. The econometrics literature has
highlighted the issues that weak instruments cause in estimation. We define a
novel concept of weak instruments for testing and show how this notion of weak
instruments relates to known degeneracy problem of RV, which has implications
for the size and power of the RV test.

One solution proposed in the weak instruments literature is to expand the
number of instruments, as this allows a more flexible prediction of the
endogenous variable in the first stage. However, while this results in better
fit of the first stage, it may lead to overfitting problems. In particular,
the econometrics literature has noted that in estimation, the use of many
instruments can bias IV estimates towards their OLS counterparts. We
demonstrate that similar issues obtain for testing.

###  6.1 The Problem with Testing without Instruments

In Section 4.4, the RV test statistic is defined using measures of fit which
are functions of excluded instruments $z$. The theoretical results obtained in
the paper rely crucially on this assumption. However, implementations of the
RV test based on residual sum of squares (RSS) have been popular in the
applied literature in industrial organization.202020For example, b87, glv92,
bd10 and Bonnet, Dubois, Villas-Boas, and Klapper (2013) use RSS-based
procedures to test hypotheses on conduct (collusion in the first two examples
and vertical markets in the others).

These RSS-based procedures are problematic and can provide misleading
implications for conduct. To illustrate why, we briefly summarize how one
could implement a test based on RSS in a model selection context. First, one
would impose model $m$ and rearrange the first order conditions of the firm as
the following linear model in $\mathbf{w}$:

$\displaystyle\mathbf{p}-\mathbf{\Delta}\theta_{m}=\mathbf{w}\tau+\bm{\omega}.$
(39)

Under the imposed model, $\mathbf{p}-\mathbf{\Delta}\theta_{m}$ is observed
and one can then obtain an OLS residual $\hat{\bm{\omega}}_{m}$ from the
regression (39). Given that the OLS regression imposes that w is orthogonal to
$\bm{\omega}_{m}$, one can equivalently set
$\hat{\bm{\omega}}_{m}=p-\Delta\theta_{m}=\hat{\omega}_{m}.$ One then
constructs for model $m$ a measure of fit
$Q_{m}^{RSS}=\frac{1}{n}\sum_{i}(\hat{\omega}_{mi})^{\prime}(\hat{\omega}_{mi})$,
and computes a test statistic analogous to (31):

$\displaystyle
T^{RSS}=\frac{\sqrt{n}}{\hat{\sigma}_{RSS}}(Q_{1}^{RSS}-Q_{2}^{RSS}),$ (40)

where $\hat{\sigma}_{RSS}$ is a consistent estimator of the standard deviation
of the difference in the RSS measures of fit. The formulation of the
hypotheses is identical to what we have described in Section 4.4, except for
the different measure of fit, making this procedure appear similar to RV.

To better understand the issues with RSS-based testing, consider alternative
moments

$\displaystyle h_{m}=\frac{\Delta^{\prime}\hat{\omega}_{m}}{n},$ (41)

which are the moments one would use to estimate Equation (3) by OLS. We define
a measure of fit using these moments as $Q_{m}^{OLS}=h_{m}^{\prime}Wh_{m}$.
Now we can prove the following lemma:

######  Lemma 2.

For any model $m$, $Q_{m}^{RSS}$ and $Q_{m}^{OLS}$ are equal up to a constant.
Hence, the RSS test statistic can be written as:

$\displaystyle
T^{RSS}=\frac{\sqrt{n}}{\hat{\sigma}_{RSS}}(Q_{1}^{OLS}-Q_{2}^{OLS}).$

The lemma establishes the equivalence between the RSS-based procedure and
testing using OLS moments. It is now easy to see that, due to the endogeneity
of markups, the population analog of moments $h_{m}$ will not be equal to zero
at the true parameter value $\theta_{m}=\theta_{0}$. Instead, $Q_{m}^{OLS}$ is
minimized for $\theta_{m}=\hat{\theta}_{OLS},$ the OLS estimator of $\theta$
in Equation (3). Hence, testing based on $T^{RSS}$ may generate tests with the
wrong size, and possibly no power against some incorrect fixed alternatives.
For example, consider the two models
$\theta_{1}=\theta_{0},\theta_{2}=\hat{\theta}_{OLS}$. As $n$ goes to
infinity, an RSS-based procedure using the statistic $T^{RSS}$ will always
reject the null of equal fit in favor of model 2, the wrong model. We
formalize this intuition in the following proposition:

######  Proposition 4.

Assume that the testing environment is TE1, true markups are not observed, and
that Assumptions 1, 2 and 5 are satisfied. Then we can derive the following
convergence in probability results for $T^{RSS}$:

$\displaystyle\frac{T^{RSS}}{\sqrt{n}}$
$\displaystyle\rightarrow_{p}\frac{E[(\Delta_{OLSi}-\Delta_{1i}))^{2}-(\Delta_{OLSi}-\Delta_{2i}))^{2}]}{\sigma^{RSS}},$
(42)

where $\Delta_{OLS}=\Delta\theta_{OLS}$ and
$\theta_{OLS}=E[\hat{\theta}_{OLS}]=A_{\Delta\Delta}^{-1}A_{\Delta p}$.

The proposition shows that the results of RSS-based tests are driven by the
relative distance of the markups implied by the two models from the OLS
predicted markups. Since $\Delta$ is generally correlated with $\omega$, the
OLS estimates of $\theta$ are inconsistent, making the OLS projections of
markups potentially far from the true markups, and thus making the test
inconsistent.

Our discussion thus far in this section is based on an RV-like test statistic
because this has been used in the applied literature. In fact, other testing
procedures (most notably, Cox and EB) could be performed using the moments $h$
based on OLS fit, thus incurring in the same problems. An obvious solution is
to test based on the correct moment $g$ by including instruments as in the
procedures described in Section 4. Proposition 1 shows that tests based on the
moment condition $g$ have the right size and are consistent for fixed
alternatives, pointing asymptotically towards the model that generates
predicted markups that are closest to the true ones.212121In this paper, we
have assumed $\Delta$ is data so that demand is known before testing supply.
Practically, one could simultaneously estimate demand and supply jointly for
the two candidate models and then do testing (see g13 as an example). For this
case, if one included enough demand instruments to overidentify the demand
parameters by two, RSS measures of fit would satisfy the exclusion
restrictions and be valid, so long as at least two of the demand instruments
satisfy Assumptions 1 and 3.

###  6.2 Weak Instruments for Testing: Degeneracy of RV

It is well known that the RV test may suffer from a degeneracy problem when
$\sigma_{RV}$ is zero. When this happens the numerator of $T^{RV}$ is also
vanishing. This leads the RV test statistic to no longer be asymptotically
normal, and the test may suffer from size distortions and low power, depending
on the relative magnitude of the numerator and denominator.

We show that degeneracy can be characterized as a problem of weak instruments
for testing. First we define a notion of weak instruments for testing:

######  Definition 1.

Instruments are weak for testing if:

$\displaystyle\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{m}=o_{p}(1)\text{ for
}m=1,2,$ (43)

where $\hat{\Gamma}^{*}_{0}$ is the projection coefficient of the true markups
$\Delta^{*}_{0}$ on instruments. For example consider
$(\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{m})=\frac{q_{m}}{\sqrt{n}}+o_{p}(n^{-1/2})$
for a finite vector $q_{m}$. This analogue to the weak instrument condition in
ss97 satisfies our definition. To see more clearly how the definition relates
to degeneracy, rewrite the numerator of $T^{RV}$ as:

$\displaystyle\sqrt{n}(Q_{1}-Q_{2})$
$\displaystyle=\sqrt{n}\bigg{(}(\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{1})-(\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{2})\bigg{)}^{\prime}\frac{z^{\prime}z}{n}\bigg{(}(\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{1})+(\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{2})\bigg{)}$
$\displaystyle\qquad\qquad+2\bigg{(}(\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{1})-(\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{2})\bigg{)}^{\prime}\frac{z^{\prime}\omega_{0}}{\sqrt{n}}.$

When $(\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{m})=o_{p}(1)$ for $m=1,2$, under the
regularity conditions of Assumption (2), $\sqrt{n}(Q_{1}-Q_{2})$ converges
quickly enough to zero, so that its asymptotic variance is zero. The following
proposition formalizes that weak instruments for testing characterize
degeneracy.

######  Proposition 5.

Suppose that Assumptions 1 and 2 hold. Then $\sigma^{2}_{RV}=0$ if and only if
$\hat{\Gamma}^{*}_{0}-\hat{\Gamma}_{m}=o_{p}(1)$ for $m=1,2$.

Thus degeneracy of the RV test concerns the first-stage coefficients of a
regression of the difference in markups implied by one of the two candidate
models and the truth on the instruments. If the ability of the instruments to
predict a nonzero difference in markups vanishes at the appropriate rate, RV
will suffer from degeneracy. Notice that as $\hat{\Gamma}_{1}$ and
$\hat{\Gamma}_{2}$ approach $\hat{\Gamma}^{*}_{0}$, the predicted markups
across models 0, 1 and 2 become indistinguishable. Thus we can express
degeneracy as a condition on predicted markups. Further note that this implies
that the null for RV is satisfied as the predicted markups for model 1 and 2
are indistinguishable. Whether the converse is true depends on the testing
environment. We formally connect the condition for degeneracy to the null
being satisfied for RV in the following corollary.

######  Corollary 5.

$\sigma^{2}_{RV}=0$ iff

  * (i)

$E[(\tilde{\Delta}_{1i}-\tilde{\Delta}_{2i})^{2}]=0$ in TE1 so that degeneracy
coincides with the null hypothesis of RV.

  * (ii)

$E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]=0$ for $m=1,2$ in TE2
and TE3 so that degeneracy is a special case of the null hypothesis of RV.

In TE1, the corollary shows that degeneracy arises whenever the null
hypothesis of RV is satisfied - which occurs when the testability condition in
Lemma 1 is violated.222222This result is in line with hp11, who note that when
both models are true, RV is degenerate. Hence, one should be particularly
concerned about degeneracy in this setting. In TE2 and TE3, the distinction
between degeneracy and the null hypothesis of RV is best understood with the
help of Figure 4.

Figure 4: Degeneracy and Null Hypothesis This figure illustrates that the
region of degeneracy is a subspace of the null space for the RV test.

In the figure we represent the space of expected square differences in
predicted markups for the two models, which corresponds to the space of
$\mathcal{Q}_{1}$ and $\mathcal{Q}_{2}$. While the null hypothesis of RV is
satisfied along the full 45-degree line, degeneracy only occurs at the origin.
Hence, in TE2 and TE3 being in the null space is necessary for degeneracy, but
not sufficient.

In our setting there are two empirically relevant cases in which degeneracy
occurs, which have been discussed separately in the econometrics literature.
The first is that the two economic models are overlapping with the truth, in
the sense of implying vectors of markups $\Delta_{1}$ and $\Delta_{2}$ that
converge to one another and to $\Delta_{0}$ quickly as the sample size gets
large. This can happen, for instance, in the profit weights model, if two
competing models specify profit weights that approach the true profit weight
asymptotically. The second is a model-specific weak instruments problem, so
that even if the two models imply different markups, $\Gamma^{*}_{0}$,
$\Gamma_{1}$ and $\Gamma_{2}=0$. This can arise, for example, in empirical
applications where the instruments are largely noise. We discuss in Section XX
how one can diagnose this issue in an empirical setting and various tools to
correct for degeneracy.

###  6.3 Many Instruments for Testing: Bias of RV

The RV test fundamentally depends on predicting markups from the instruments.
When the first stage is viewed in this light, one may consider adding a large
number of instruments in order to improve the predictions. In light of
Proposition 5, there may be benefits to doing so in the context of RV.
However, this comes at a cost. The econometrics literature has discussed the
problem of many instruments in an estimation context. Specifically b94 and
cs05, by using a many instrument asymptotic, so that the 2SLS estimator is
inconsistent. More troubling, this asymptotic has been found to approximate
well the finite sample distribution of the estimator, thus revealing
substantial bias towards the OLS estimator. The intuition, discussed in ad09
is that, by increasing the number of instruments, one overfits the endogenous
variable. In the extreme, one predicts the endogenous variable perfectly and
thus reverts to OLS in the second stage.

We provide new results showing the impact of many instruments on the RV test.
To do so, we consider a many instrument asymptotic, following b94 and cs05.
Specifically, we assume the following:

######  Assumption 10.

Let the number of instruments grow at rate $n$ so that
$\frac{d_{z}}{n}\rightarrow_{p}\delta_{z}>0$. Moreover, suppose:

  * (i)

$\frac{\hat{\Gamma}^{\prime}z^{\prime}z\hat{\Gamma}}{n}\rightarrow H+o_{p}(1)$

  * (ii)

$\frac{\hat{\Gamma}^{\prime}z^{\prime}z\hat{\Gamma}^{*}}{n}\rightarrow
H^{*}+o_{p}(1)$

for some matrices $H,H^{*}>0$.

The above assumption maintains that as the number of instruments grows, the
concentration parameters $\frac{\Gamma^{\prime}z^{\prime}z\Gamma}{n}$ and
$\frac{\Gamma^{\prime}z^{\prime}z\Gamma^{*}}{n}$ are non-diverging. There are
several ways to interpret this. First is that the variance of the predicted
markups remains finite as the number of instruments approaches infinity. This
means that, eventually, additional instruments are uninformative in predicting
markups. Regardless of the interpretation, the econometrics literature has
found that the asymptotic distribution obtained with this assumption is a very
good approximation of the finite sample performance with man instruments (see
ak95).

Under Assumption 10, we can characterize the behavior of the RV test statistic
in a many instrument setting. Specifically, we derive the following
convergence in probability result.

######  Proposition 6.

Suppose that the markups $\Delta^{*}$ are unobserved and that Assumptions 1,
2, and 10 are satisfied. Then:

$\displaystyle\frac{T^{RV}}{\sqrt{n}}\rightarrow_{p}$
$\displaystyle\frac{1-\delta_{z}}{\sigma_{RV}}\bigg{(}E[(\tilde{\Delta}_{1i}-\tilde{\Delta}^{*}_{0i})^{2}]-E[(\tilde{\Delta}_{2i}-\tilde{\Delta}^{*}_{0i})^{2}]\bigg{)}$
$\displaystyle\qquad+\frac{\delta_{z}}{\sigma_{RV}}\bigg{(}E[(\Delta_{1i}-\Delta_{OLS,i})^{2}]-E[(\Delta_{2i}-\Delta_{OLS,i})^{2}]\bigg{)}$

Proposition 6 sheds light on important aspects of testing with many
instruments. Just as in estimation, we see that the RV test is biased towards
the RSS test discussed in Section 6.1, which forms the moments with the
endogenous markups. The extent of the bias depends on the magnitude of
$\delta_{z}$. h20 states that although there is no set rule of thumb, many
instruments are a serious concern whenever the number of instruments exceeds
5% of the sample size. However, many instruments can still create significant
bias below that threshold. In fact, ak95 find severe bias in a setting where
$\frac{d_{z}}{n}$ is as small as 0.5%.

Thus, a researcher should be concerned when using many instruments even if
they are valid. While valid instruments implement the condition in Lemma 1,
there is no guarantee that using them to form the RV test will allow one to
achieving correct inference either in finite sample or asymptotically. We
return to the problem of many instruments in Section XX and propose a
modification of the RV test statistic which removes the finite sample bias
they cause.

##  7 Step by step implementation of our preferred RV procedure

In this section we discuss practical considerations in implementing RV,
following the steps that researchers will need to take. These are: (i)
estimating demand with or without supply moments, (ii) choosing instruments,
(iii) choosing a weight matrix, (iv) extending RV testing to more than two
conduct models, and (v) enhancing the interpretability of the test by
visualizing the absolute fit of each model and diagnosing potential issues. We
consider these in turn.

###  7.1 Step 1 - Demand Estimation: Sequential versus Simultaneous

When performing testing for conduct in an environment such as the one
described in Section 2, the researcher has to first estimate demand to obtain
measures of markups $\Delta_{m}$ for each conduct model $m$. Although
estimation of demand is often described as a preliminary step, it does not
have to be: demand estimation and testing can be performed simultaneously. In
a GMM setting, this is immediate as demand moments are simply stacked together
with supply moments, and fit is evaluated globally for all moments. While the
issue of simultaneous versus sequential estimation has been thoroughly
discussed in the literature on demand estimation, we focus here on the
implications for testing conduct.

To illustrate this issue, consider a setting where testing is performed in a
GMM environment and the supply moments for any model of conduct $m$ are:

$\displaystyle g_{m}\left(\theta^{D}\right)$
$\displaystyle=\frac{1}{n}z^{\prime}(p-\Delta(\theta^{D})\theta_{m}),$

which formalizes that the supply moments in Equation (8) depend on demand
parameters $\theta^{D}$ through markups, or $\Delta=\Delta(\theta^{D})$.
Demand moments are:

$h\left(\theta^{D}\right)=\frac{1}{n}\textbf{z}^{D\prime}\bm{\xi}(\theta^{D}),$

where $\bm{\xi}(\theta^{D})$ is the value of the demand unobservable implied
by the data and by the parameter value $\theta^{D}$, and $\textbf{z}^{D}$ is a
vector of demand instruments.232323Demand moments could include micro-moments
that make use of additional data sources. All of our discussion in this
section would go through in this case. We assume that the dimension of
$\textbf{z}^{D}$ is sufficient for identification of $\theta^{D}$ from demand
moments alone. To estimate $\theta^{D}$, one can thus ignore the supply side,
form a weight matrix
$W^{D}=(\frac{\textbf{z}^{D\prime}\textbf{z}^{D}}{n})^{-1}$ and construct the
objective function

$\displaystyle Q^{D}(\theta^{D})=h(\theta^{D})^{\prime}W^{D}h(\theta^{D}).$
(44)

We can then define $\theta^{Dseq},$ the asymptotic value of the demand
parameters obtained with the sequential method as:

$\displaystyle\theta^{Dseq}=\arg\min_{\theta^{D}}\mathcal{Q}^{D}(\theta^{D}),$

where $\mathcal{Q}^{D}=plimQ^{D}$. After having estimated demand, in a
sequential step we construct the RV statistic for testing conduct by
evaluating the supply GMM objectives corresponding to each model $m$, whose
asymptotic value is:

$\mathcal{Q}_{m}(\theta^{Dseq})=\mathcal{g}_{m}(\theta^{Dseq})^{\prime}W\mathcal{g}_{m}(\theta^{Dseq}).$

Alternatively, we could use the supply moments in estimating demand by
stacking all moments. The corresponding simultaneous GMM objective function
is:

$\displaystyle Q_{m}^{sim}(\theta^{D})$
$\displaystyle=\left[\begin{array}[]{c}g_{m}(\theta^{D})\\\
h(\theta^{D})\end{array}\right]^{\prime}W^{sim}\left[\begin{array}[]{c}g_{m}(\theta^{D})\\\
h(\theta^{D})\end{array}\right].$

To simplify the problem in a way that we can tractably analyze the
implications for testing, we maintain the following assumption on $W^{sim}$:

######  Assumption 11.

$W^{sim}$ is block diagonal, so that $W^{sim}=\begin{bmatrix}W&0\\\
0&W^{D}\end{bmatrix}$.

In this simple case the simultaneous GMM objective function is:

$Q^{sim}_{m}\left(\theta^{D}\right)=Q_{m}(\theta^{D})+Q^{dem}\left(\theta^{D}\right),$

so that the asymptotic value of the demand parameters with the simultaneous
approach is given as:

$\theta_{m}^{Dsim}=\arg\min_{\theta^{D}}\mathcal{Q}_{m}(\Delta(\theta^{D}))+\mathcal{Q}^{dem}(\theta^{D}).$

Notice that, while $\theta^{Dseq}$ does not depend on a model of conduct $m$,
the value of $\theta_{m}^{Dsim}$ is specific to model $m$.

We can then establish the following result:

######  Proposition 7.

Suppose that Assumption 11 holds, that $\theta_{m}^{Dsim}$ is unique, and
$\theta^{Dseq}\neq\theta_{m}^{Dsim}$ for $m=1,2$. Then,

  1. 1.

in any environment where cost shifters are correctly specified as w:

$\displaystyle
E[(\tilde{\Delta}^{*}_{0}-\tilde{\Delta}_{m}(\theta_{m}^{Dsim}))^{2}]<E[(\tilde{\Delta}^{*}_{0}-\tilde{\Delta}_{m}(\theta^{Dseq}))^{2}];$

  2. 2.

in any environment where cost shifters $\textbf{w}_{a}$ are not correctly
specified, but for which Assumption 8 holds:

$\displaystyle
E[(\tilde{\Delta}^{C}_{0}-\tilde{\Delta}_{m}(\theta_{m}^{Dsim}))^{2}]<E[(\tilde{\Delta}^{C}_{0}-\tilde{\Delta}_{m}(\theta^{Dseq}))^{2}]$

where
$\Delta^{C}_{0}=M_{\textbf{w}_{a}}(\bm{\Delta}_{0}^{*}+\textbf{w}\tau-\textbf{w}_{a}\tau_{a})$.

The consequences of this proposition vary depending on the model of conduct
$m$ and on the testing environment. In TE1, for $m=1$ we have that
$\theta^{Dseq}=\theta_{1}^{Dsim}$, and
$E[(\tilde{\Delta}_{0}-\tilde{\Delta}_{1}(\theta_{1}^{Dsim}))^{2}]=E[(\tilde{\Delta}_{0}-\tilde{\Delta}_{1}(\theta^{Dseq}))^{2}]=0.$
Hence, in TE1, $\mathcal{Q}_{1}-\mathcal{Q}_{2}$ gets smaller in magnitude
when adopting a simultaneous approach. In TE2 when only demand is misspecified
the proposition implies that the bias is smaller with a simultaneous approach,
thus bringing predicted markups for model 1 closer to the true ones. However,
predicted markups for $m=2$ also get closer to the true ones. This may not be
desirable if the fit for the wrong model of conduct improves much more than
the fit for the correct model. If the researcher maintains the assumption that
the testing environment is low-bias in the sense of Assumption 6, and has a
large dataset, a simultaneous approach may change the sign for the RV
statistic - thus causing the researcher to conclude in favor of the wrong
model of conduct. However, if Assumption 6 is violated or if the dataset is
small, a simultaneous approach may offer advantages in terms of reducing bias.
Also in TE3, the simultaneous approach generates predicted markups closer to
the true predicted markups for both models when cost is not misspecified.

Instead, when cost is misspecified, the simultaneous approach pulls the
predicted markups for both models towards the predicted markups
$\tilde{\Delta}^{C}_{0}$ that satisfy the exclusion restriction. As is also
true when cost is correctly specified, a simultaneous approach provides a
better fit for both models. Similar to the discussion above, if the
simultaneous approach improves the fit of the true model relative to the wrong
model, then it is to be preferred. However, there is no guarantee that this
will obtain in a specific empirical setting. We summarize these findings in
the following corollary:

######  Corollary 6.

Suppose that Assumption 11 holds, and that $\theta_{m}^{Dsim}$ is unique and
$\theta^{Dseq}\neq\theta_{m}^{Dsim}$ for $m=1,2$. Then:

  * •

In TE1, the plim of the numerator of the RV test statistic is smaller in
magnitude under simultaneous estimation, but maintains the same sign as under
sequential estimation.

  * •

In TE2 when demand is misspecified, simultaneous estimation reduces bias.

  * •

In TE2 if either demand or costs are misspecified, or in TE3, the sign and
magnitude of the numerator of the RV test statistic could differ under
simultaneous and sequential approaches.

In addition to affecting the numerator of the RV test statistic, the choice
between simultaneous and sequential approaches has an impact on the
denominator as well. However, even under Assumption 11 and in a TE1
environment, this effect is ambiguous242424We leave it to future research to
fully characterize the effects on efficiency.

It is interesting to draw a parallel between the effects of simultaneous
estimation on markups, and the effects on parameter estimates - especially,
demand parameters. The literature on demand estimation (see cg19) has
discussed in particular two aspects of this choice. The first is the relative
efficiency of the two approaches. Simultaneous estimation is more efficient
under the assumption of no misspecification and using an optimal GMM weight
matrix. These considerations do not immediately apply to our setup, where even
in TE1 one of the models of conduct that we consider is not correctly
specified. The second aspect concerns whether the inclusion of supply moments
for the correct model improves the demand estimates. Our result shows that
adding supply moments pulls the demand parameters towards regions where the
predicted markups under the assumed conduct model are closer to the predicted
markups satisfying the exclusion restrictions. There is no guarantee that
simultaneous estimation will result in demand parameter estimates which are
closer to the true demand parameters.

###  7.2 Step 2 - Choosing Exogenous Variables

We discuss in this section what types of identifying variation a researcher
should look for in the data. When discussing the vector of instruments $z$ in
Section 2, we did not take a stand on its components. Instead, we defined
$z=Z(\bar{z})$ where $\bar{z}$ are exogenous variables in the data. As we saw
in Figure 1, it is movement in the demand curve across many markets that
allows us to distinguish models of conduct, and such movement is induced by
variables that shift and rotate the demand curve. As originally pointed out in
b82, rotators are necessary when demand and marginal costs are linear.
Alternatively, demand shifters may be sufficient.

The choice of these shifters and rotators depends on the economics of the
problem. Conveniently, the shifters and rotators needed to test firm conduct
are the same variables that can be used to identify the heterogeneity of
random coefficients in blp95 demand systems. bh14 describe standard sources of
exogenous variation that can be used in testing: variation in the number of
competing firms or products, characteristics of competing products, market
size, and costs of competing firms. Other market-level demographics can be
also used as demand rotators, in the spirit of w03. Since in some setting the
variation in firms and products is limited, gh19 emphasize the role of
interacting market-level demographics with variation in the sets of rival
products. Specific applications may suggest further sources of exogenous
variation $\bar{z}$.

To satisfy assumptions 1 and 3, the instruments constructed using the
variation in $\bar{z}$ need to satisfy two requirements. The first is that
they must be exogenous for testing, in the sense of being uncorrelated with
the cost shifters for the true model. Since either of the two candidate models
that we want to test could be the true one, we must select $\bar{z}$ variables
that can be used to form valid instruments for either - and this requirement
may not be trivial. For instance, if one of the candidate models of conduct
specifies the simultaneous choice of products and prices, standard BLP or
differentiation instruments, constructed from variation in product
characteristics, could not be used, as the variables on product
characteristics are not exogenous.

Additionally, instruments need to be relevant for testing, in the sense of
generating different predicted markups for the two candidate models. Notice
that even models that imply zero or constant markups can be tested against
another model for which markups do vary with the instruments. In fact, even
instruments that are orthogonal to markups for one model could be used for
testing. For example, in the canonical example considered in b82 where one of
the models is perfect competition, testing is still feasible because the
alternative model, monopoly, generates markups that are correlated with the
instruments.

###  7.3 Step 3 - Forming the Instruments

Once one chooses the set of demand shifters and rotators $\bar{z}$, then one
can use them to form the instruments $z$. A common choice is to use the
shifters directly as instruments, specifying $z=\bar{z}$. In an ideal setting,
$\bar{z}$ predict markups for the two models which are sufficiently distinct
as to permit the researcher to reject the null, and potentially creating the
inferential problems linked to weak instruments for testing. Thus, in practice
one may want to improve the prediction of the markups by specifying $z$ more
flexibly from the data. As the cost shifters also enter the first stage,
similar considerations apply to the specification of w from the data.252525As
discussed in Section 5.3 one may want to flexibly specify marginal cost from
the data on cost shifters to reduce misspecification. To implement this
flexibility in our setting, define $\textbf{w}=\mathbf{W}(\bar{\textbf{w}})$,
where $\bar{\textbf{w}}$ are variables in the data that shift cost. The non-
orthogonalized version of the first order conditions in Equation (2) are:

$\displaystyle\mathbf{p}=\bm{\Delta}_{m}+\mathbf{W}(\bar{\textbf{w}})\tau+\bm{\omega}_{m},$

Suppose now that the first stage equation for markups is estimated with a
sieve regression model, or:

$\displaystyle{\bm{\Delta}}_{m}$
$\displaystyle=\mathbf{Z}(\bar{\mathbf{z}},\bar{\textbf{w}})\bm{\Gamma}_{m}+\mathbf{W}(\bar{\textbf{w}})\bm{\beta}_{m}+e_{m}$
(45)

where for a sieve expansion $\mathbf{Z}(\bar{\mathbf{z}},\bar{\textbf{w}})$,
we can define the $d_{z}\times 1$ vector of instruments
$\mathbf{z}_{i}=\mathbf{Z}(\bar{\mathbf{z}_{i}},\bar{\textbf{w}_{i}}).$ We
assume that the basis function is such that there are functions $\mathbf{W}$
that depend on $\bar{\textbf{w}}$ only.262626This is not necessary for the
argument to go through, but convenient as it allows us to orthogonalize all
variables with respect to $\textbf{w}=\mathbf{W}(\bar{\textbf{w}})$. We assume
that Assumption 1 holds for our choices of $\bar{\mathbf{z}},\bar{\textbf{w}}$
and $\mathbf{Z},\mathbf{W}$.

One way to interpret this process is through its effect on the vector of
predicted markups $\tilde{\Delta}=z^{\prime}\Gamma$. Although $\tilde{\Delta}$
is a linear projection on instruments, flexibility in the choice of $z$ can
result in predicted markups that are highly nonlinear in the original demand
shifters and rotators. bcs20 are the first to highlight the importance of
flexibility in the choice of instruments and cost shifters, and show how it
contributes to distinguishing the predicted markups generated by the two
models.272727Instead of a sieve expansion, bcs20 use a random forest algorithm
to predict the difference in markups implied by the two models.

While in general flexibility may be desirable, if the first stage is specified
too flexibly, it can result in overfitting. This issue has been discussed
extensively in the literature on many instruments. As we showed in Proposition
XX, the use of many instruments in our testing environment biases the RV test
statistic toward the RSS test. Several solutions have been offered to the
problem of many instruments in an estimation setting. af19 compare several,
and find that the improved jackknife instrumental variables estimator perform
particularly well. Proposed by ad09, IJIVE avoids overfitting the predicted
markups by running a leave one out regression in the first stage. Furthermore,
ad09 recommend otrhogonalizing the data with respect to exogenous regressors
before running IJIVE as this further reduces finite sample bias. This fits
well in our setting where all variables are othogonalized with respect to w.

Here, we propose a version of the RV test inspired by IJIVE. In particular we
define the measure of fit:

$\displaystyle Q^{IJIVE}_{m}$
$\displaystyle=\frac{1}{n}\omega_{m}^{\prime}C^{\prime}C\omega_{m}$ (46)

where $C=(I-D_{P_{z}}+\frac{3}{n}I)^{-1}(P_{z}-D_{P_{z}}+\frac{3}{n}I)$.
Notice that $Q^{IJIVE}_{m}$ is similar to $Q_{m}$. $Q^{IJIVE}_{m}$ replaces
$P_{z}$ with $C$ a modified version of $P_{z}$ which implements the leave-one-
out first stage and removes any remaining bias.It is easy to derive the plim
of the RV test statistic based on IJIVE:

$\displaystyle\frac{T^{RV,IJIVE}}{\sqrt{n}}$
$\displaystyle\rightarrow_{p}\frac{E[(\tilde{\Delta}^{IJIVE}_{0i}-\tilde{\Delta}^{*,IJIVE}_{1i})^{2}]-E[(\tilde{\Delta}^{*,IJIVE}_{0i}-\tilde{\Delta}^{IJIVE}_{2i})^{2}]}{\sigma_{RV,IJIVE}}$
(47)

This is an exact anlogue of the result in Propositon 2. Now, instead of
generating $\tilde{\Delta}=P_{z}\Delta$, predicted markups are generated as
$C\Delta$. $C$ performs the leave one out regression of $\Delta$ on $z$. Both
tests reject in favor of the model for which the predicted markups are closer
to the truth. In the empirical example, we show the performance of
$T^{RV,IJIVE}$ relative to $T^{RV}$ in a setting with many instruments,
highlighting the importance of bias correction when the number of instruments
is large.

[maybe put in a bit more of the flavor of on the one hand you have bias to
RSS, on the other you have degeneracy…check in papers in the lit, use it to
better justify IJIVE]

###  7.4 Step 4 - Choosing the Weight Matrix

An important aspect of the RV testing procedure we described in Section 4 is
the choice of the weight matrix.282828However, this is also true of Cox, EB,
and AR - changing the weight matrix may have a substantial impact on these
test statistics. As we argue below for RV, choosing $W=\hat{A}^{-1}_{zz}$ for
EB and Cox results in interpretable links between the asymptotic results of
these tests and the Euclidean distance between the predicted markups implied
by each model and the truth. Since we are in a GMM setup, one may think that
the usual considerations based on efficiency that are invoked in the choice of
weight matrix, apply here. However, using an approximation to the optimal
matrix in estimation can work poorly in finite sample (e.g. ab91) or when
models are misspecified (hi03), and furthermore in our testing environment the
notion of efficiency is not straightforward.

We adopt throughout the weight matrix $W=\hat{A}_{zz}^{-1},$ which results in
an interpretable comparison between models of conduct: as shown in
Propositions 1 and 2, RV concludes asymptotically in favor of the model whose
predicted markups are closer to the true ones in the sense of Euclidean
distance. hp11 highlight that the RV testing procedure is sensitive to the
choice of weights. In fact, when choosing a weight matrix $W$ different from
$\hat{A}_{zz}^{-1}$, Propositions 1 and 2 can be easily modified to show that:

$\displaystyle\frac{T^{RV}}{\sqrt{n}}$
$\displaystyle\rightarrow_{p}\frac{E[(\tilde{\Delta}_{1i}-\tilde{\Delta}^{*}_{0i})z_{i}Wz_{i}(\tilde{\Delta}_{1i}-\tilde{\Delta}^{*}_{0i})]-E[(\tilde{\Delta}_{2i}-\tilde{\Delta}^{*}_{0i})z_{i}Wz_{i}(\tilde{\Delta}_{2i}-\tilde{\Delta}^{*}_{0i})]}{\sigma_{RV}}.$

This expression shows that adopting a generic $W$ weight matrix makes the RV
test asymptotically conclude in favor of the model whose predicted markups are
closer to the true predicted markups based on a distance measure defined by
$W$. In general, we see no reason not to prefer the Euclidean distance, which
results in intuitive comparisons. In fact, we showed in Lemma 1 that the ideas
of testability of models of conduct in b82 and bh14 naturally involve in our
setup the evaluation of the Euclidean distance in predicted markups.

The choice of weight matrix could also have another important effect on the RV
test: changing when degeneracy of the test statistic occurs. For instance,
consider the following weight matrix:

$\displaystyle\widetilde{W}=(\hat{\Gamma}_{1}-\hat{\Gamma}_{2})(\hat{\Gamma}_{1}-\hat{\Gamma}_{2})^{\prime}.$
(48)

If one is flexible in the choice of instruments as discussed in Section
LABEL:sec:instruments, this weight matrix can be used to construct the version
of the RV test described by bcs20:

$\displaystyle\widetilde{T}^{RV}$
$\displaystyle=\frac{\sqrt{n}(g_{1}\widetilde{W}g_{1}-g_{2}\widetilde{W}g_{2})}{\hat{\tilde{\sigma}}}$
$\displaystyle=\frac{\sqrt{n}((\tilde{\Delta}_{1}-\tilde{\Delta}_{2})^{\prime}\omega_{1})^{2}-(\tilde{\Delta}_{1}-\tilde{\Delta}_{2})^{\prime}\omega_{2})^{2})}{n\hat{\tilde{\sigma}}},$

which uses an analogue to the c87 optimal instruments for testing. In Appendix
B, we show how this formulation relates to $T^{RV}$ defined with the
$W=\hat{A}_{zz}^{-1}$ weight matrix. As long as $\widetilde{T}^{RV}$ is not
degenerate, the two test statistics are identical, and thus asymptotically
rely on the comparison of Euclidean distances in predicted markups. However,
this alternative formulation of the weight matrix can result in
$\widetilde{T}^{RV}$ being degenerate when $T^{RV}$ is not. To see this point,
recall that the condition for degeneracy of $T^{RV}$ in Proposition 5 occurs
when $\hat{\Gamma}_{1}$ and $\hat{\Gamma}_{2}$ approach each other, and also
approach $\hat{\Gamma}^{*}_{0}$. Instead, it is easy to see from the
formulation of $\widetilde{W}$ that whenever $\hat{\Gamma}_{1}$ and
$\hat{\Gamma}_{2}$ approach each other, $\widetilde{W}$ approaches the zero
matrix, thus causing degeneracy of $\widetilde{T}^{RV}$.

Figure 5: Weight Matrix and Degeneracy This figure illustrates: (i) the region
where the null of the RV test is satisfied, represented by the two 45-degree
lines, (ii) the region of degeneracy for $\widetilde{T}^{RV}$ on the red
dashed 45-degree line, and (iii) the region of degeneracy for $T^{RV}$ at the
origin.

While the discussion in Appendix B holds in general, we can visualize the
comparison of the spaces of degeneracy in a figure for the simple case of one
instrument. Since $\Gamma_{m}$ is a scalar, in Figure 5 we plot the space with
coordinates $\Gamma^{*}_{0}-\Gamma_{m}$ for $m=1,2$. The null of RV
corresponds to both 45-degree lines. Degeneracy of $\widetilde{T}^{RV}$ occurs
along the positive 45-degree red dashed line, whereas degeneracy of $T^{RV}$
only occurs at the origin. In practice, expanding the region of degeneracy of
the test may be relevant. For instance, consider a situation where the two
models approach each other, but are far from the truth, possibly because of
misspecification in demand or cost. In this case, $\widetilde{T}^{RV}$ will be
degenerate (with problematic consequences for the size and power of the test)
but $T^{RV}$ will not be.

###  7.5 Step 5 - Running the RV test with Two or More Models of Conduct

While our discussion so far has concerned the comparison of two models of
conduct, we show here that the RV test can be extended to settings with
multiple models. In empirical work, researchers often have more than two
models of conduct that they want to test (for instance see v07, bd10, and
bcs20). In many of these papers, the researchers perform pairwise tests across
all models and report all the test statistics in a table. One should interpret
such a table with caution. In particular, problems with testing in this manner
can arise because the RV test statistic may not be transitive (although the
comparison of numerators of RV is transitive). Furthermore, this procedure
does not control for the familywise error rate (FWE), that is the probability
of rejecting at least one true null. For example, the probability of rejecting
the true model against any wrong model is increasing in the number of models
considered.

We propose instead that the researcher implement the Model Confidence Set
(MCS) procedure in hln11. These authors develop a sequential testing method,
suited for model selection, that delivers a set of models for which one cannot
reject the null that they fit equally well. More formally, suppose that the
researcher wants to test a set $\mathcal{M}$ of models, each characterized by
an objective function $Q_{m}$. For any two models $j,k$ we can define the RV
test statistic $T_{j,k}^{RV}$. The MCS procedure tests a sequence of nulls of
the form:

$\displaystyle H_{0,\mathcal{M}^{\prime}}:T_{j,k}^{RV}=0\qquad\text{ for all
}j,k\in\mathcal{M}^{\prime}$ (49)

where $\mathcal{M}^{\prime}$ is a subset of $\mathcal{M}$. The procedure
starts with $\mathcal{M}^{\prime}=\mathcal{M}$, evaluates all the RV
statistics and finds the biggest one, or

$\displaystyle T_{max,\mathcal{M}}^{RV}=\max_{j,k\in\mathcal{M}}\mid
T_{j,k}^{RV}\mid.$ (50)

It then compares $T_{max,\mathcal{M}}^{RV}$ with the $(1-\alpha)$ quantile of
its bootstrap distribution to determine whether to reject the null. If the
null is rejected, then the procedure defines a new set
$\mathcal{M}^{\prime}=\mathcal{M}\setminus e_{\mathcal{M}}$, where
$e_{\mathcal{M}}=\arg\max_{j\in\mathcal{M}}\sup_{k\in\mathcal{M}}T_{j,k}^{RV}$,
and the procedure continues iteratively. If at any step the null is not
rejected, then one concludes that the corresponding subset
$\mathcal{M}^{\prime}$ coincides with the model confidence set denoted
$\mathcal{M}^{*}$. Intuitively, the procedure finds, at each step, the model
that is most definitively rejected, and excludes it from the set of models
under consideration. The procedure stops when no remaining model can be
rejected in pairwise comparisons with sufficient confidence. Note that when
there are two models remaining, the procedure performs an RV test.

The resulting confidence set $\mathcal{M}^{*}$ has the appealing property that
asymptotically it contains the model(s) $m$ whose predicted markups are
closest to the true predicted markups with probability at least $1-\alpha$.
Moreover, any other model is not included in $\mathcal{M}^{*}$ with
probability that approaches one as the sample size goes to infinity. Suppose
the environment is TE1 and the condition of Lemma 1 holds. Then
$\mathcal{M}^{*}$ will asymptotically contain only the true model as all the
other models will have predicted markups that are different from the truth.
Likewise, in TE2, so long as the true model has lower bias than any other
model, then $\mathcal{M}^{*}$ will contain only the true model asymptotically.
In finite sample, whether $\mathcal{M}^{*}$ contains one or more models
depends on the informativeness of the data. Thus, considerations on the choice
of instruments and weight matrices, discussed above, are relevant.

There are two interesting cases to consider in comparison to the current
practices in the literature. Typically, researchers conclude in favor of a
model if it wins all pairwaise comparisons. While this model will be contained
in the MCS, it is not guaranteed to be the unique model in that set.
Conversely, there could be models which lose some pariwise comparisons. While
the researcher may want to conclude against those models, they may end up as
the only model in the model confidence set. For a researcher looking to
implement the MCS procedure, hln11 provide an online appendix which describes
the implementation of their procedure step by step. We show the usefulness of
the MCS procedure in our application.

###  7.6 Step 6 - Evaluate Absolute versus Relative Fit

A limitation of RV is it may conclude in favor of a model that, while
relatively better in terms of asymptotic fit, may be far from the truth. Given
the progress in estimating demand and costs, we believe that in practice
researchers will find themselves often in a low-bias environment. However, it
may still be advisable to present additional information beyond the results of
RV testing.

For instance, performing an estimation exercise in addition to RV testing can
be highly informative. Ideally, we would compute
$E[(\tilde{\Delta}^{*}_{0i}-\tilde{\Delta}_{mi})^{2}]$ for the candidate model
$m$ selected by the RV test, allowing us to learn the absolute fit of this
model. However, this is infeasible. Instead, we can estimate $\hat{\theta}$
via 2SLS and compute predicted markups for the model implied by $\hat{\theta}$
as $\tilde{\Delta}_{2SLS}=\tilde{\Delta}\hat{\theta}$. This serves as an
estimate of the true predicted markups.292929Alternatively, Proposition 2
shows that one could estimate the same measure of absolute fit by rescaling
the magnitudes of the EB and AR statistics. Note that in TE1, $\hat{\theta}$
is a consistent estimator of $\theta_{0},$ whereas, in TE2 and TE3
$\hat{\theta}$ converges in probability to $\lambda\theta_{0},$ for
$\lambda=E[\Delta_{i}\Delta_{i}^{\prime}]^{-1}E[\Delta_{i}\Delta^{*\prime}_{i}]$.303030See
Appendix A.5 for a proof. However, we show in the following Proposition that
in any environment, $\tilde{\Delta}_{2SLS}$ represents a consistent estimate
of true predicted markups $\tilde{\Delta}^{*}_{0}$.

######  Proposition 8.

Suppose that the markups $\Delta^{*}$ are unobserved and that Assumptions 1
and 2 are satisfied. Then
$\hat{\tilde{\Delta}}^{*}_{2SLS}\rightarrow_{p}\tilde{\Delta}^{*}_{0}$

The intuition for the result in Proposition 8 is based on the discussion in
Section 7.1. The supply moments used to estimate $\theta$ depend on the
distance between the predicted markups implied by $\theta$ and the true
predicted markups. The moment condition is satisfied for the value of $\theta$
where the predicted markups match the truth. In cases where $\Delta$ is
misspecified, $\theta$ is inconsistent for the truth precisely because it
adjusts to make the predicted markups match the truth asymptotically.

Hence, the sample analogue of
$E[(\tilde{\Delta}_{2SLSi}-\tilde{\Delta}_{mi})^{2}]$ can provide a feasible
way of evaluating absolute fit. In order to visualize absolute fit, we
recommend the researcher plot the distributions of $\hat{\tilde{\Delta}}_{1}$,
$\hat{\tilde{\Delta}}_{2}$, and $\hat{\tilde{\Delta}}_{2SLS}$ to visually
inspect how the predicted markups differ. While we do not have rigorous
definition of good or poor absolute fit, we suggest two possible heuristics
which can be observed on the graphs. As
$E[(\tilde{\Delta}_{2SLSi}-\tilde{\Delta}_{mi})^{2}]$ is measured in dollars-
squared, one could compare its square root to average prices observed in the
data. If the absolute fit of the predicted markups is a small fraction of the
average price, one could conclude that absolute fit is good. Alternatively,
one could compare the relative fit of the two models to the absolute fit of a
model to the truth. If model 1 is much closer to the truth than it is to model
2, this suggests that model 1 has good absolute fit. We illustrate the
usefulness of this heuristic procedure in our empirical application.

Once a researcher has decided on a heuristic, there are three cases she can
encounter. First, the model selected by RV has good absolute fit while the
alternative model has poor absolute fit. As long as the researcher believes
that the degree of misspecification is not too large, this additional evidence
supports the conclusions of the RV test. Second, the model selected by RV has
poor absolute fit. In that case, while it is possible that the model is still
true, misspecification should be a primary concern and one may want to revisit
the specification of demand and cost. Finally, both models could have good
absolute fit. In this case, one should be concerned about the choice of
instruments. In particular, overlapping models and/or weak instruments would
result in both candidate models fitting well in an absolute sense, while also
causing the RV statistic to be degenerate.

###  7.7 Step 7 - Diagnose Degeneracy

As shown in Proposition 5, degeneracy is equivalent to weak instruments for
testing. In turn, this condition is related to the magnitudes of coefficients
in two first stage regressions. Hence, similar to the current practice for
diagnosing weak instruments for estimation, reporting F statistics of first
stage regressions can be useful. Although in our case the first stage that
characterizes weak instruments is unfeasible, its F statistic can be
estimated.

Thus, consider the infeasible regression of $\Delta_{m}-\Delta_{0}$ on
instruments. The corresponding test statistic is:

$\displaystyle F_{m0}$
$\displaystyle=\frac{(\hat{\Gamma}_{m}-\hat{\Gamma}_{0})^{\prime}z^{\prime}z(\hat{\Gamma}_{m}-\hat{\Gamma}_{0})}{d_{z}\hat{\sigma}^{2}_{e_{m}0}},$
$\displaystyle=\frac{n}{d_{z}}\frac{n^{-1}\sum_{i}(\hat{\tilde{\Delta}}_{mi}-\hat{\tilde{\Delta}}^{*}_{0i})^{2}}{\hat{\sigma}^{2}_{e_{m}0}},$

where $\hat{\sigma}^{2}_{e_{m}0}$ is the sample variance of the first stage
error term. In Proposition 8, we show that $\hat{\tilde{\Delta}}_{2SLS}$
consistently estimates $\tilde{\Delta}^{*}_{0}$, so that the feasible object

$\displaystyle F_{m,2SLS}$
$\displaystyle=\frac{(\hat{\Gamma}_{m}-\hat{\Gamma}_{2SLS})^{\prime}z^{\prime}z(\hat{\Gamma}_{m}-\hat{\Gamma}_{2SLS})}{d_{z}\hat{\sigma}^{2}_{e_{m},2SLS}}$
$\displaystyle=\frac{n}{d_{z}}\frac{n^{-1}\sum_{i}(\hat{\tilde{\Delta}}_{mi}-\hat{\tilde{\Delta}}^{*}_{2SLS,i})^{2}}{\hat{\sigma}^{2}_{e_{m},2SLS}},$

represents an estimate of $F_{m}0$. In the case of weak instruments for
testing, where $(\hat{\Gamma}_{m}-\hat{\Gamma}_{0})=o_{p}(1)$ for $m=1,2$, the
F statistic $F_{m0}$ \- and hence its feasible approximation $F_{m,2SLS}$ \-
will not diverge asymptotically. However, as in the literature on weak
instruments for estimation, we cannot evaluate the null that instruments are
weak for testing by comparing both of the two $F_{m,2SLS}$ statistics to the
standard F distribution critical values.

This suggests that, whenever both F statistics are "small" and we are in large
sample, degeneracy should be a concern. If one considers each of the
regressions separately, Stock and Yogo (2005), Montiel-Olea and Pflueger
(2013) and Lee et al. (2020) propose different critical values for the F
statistic to evaluate IV estimates. While we do not characterize formally the
critical values for our setup, the thresholds in the existing literature can
provide some heuristic guidance on when we should be concerned about
degeneracy.

The econometrics literature has explored the degeneracy problem, and proposed
procedures to formulate the test statistic when $\sigma^{2}_{RV}=0$. v89 and
rv02 propose a pretest of $\sigma^{2}_{RV}=0$, but such procedure can result
in power losses. To address this, s15 and sw17 propose modifications of the
original v89 test which can be adapted to our context and help control size
distorsions while restoring some power. In ongoing work (Magnolfi, Soelvesten,
and Sullivan (2021)), we are exploring an alternative model selection
procedure that is robust to instruments which are weak for testing.
Preliminary results suggest that this procedure will maintain size control
while achieving substantial power improvements over existing approaches in the
literature.

Notice that the standard F statistic of the first stage for model $m$ can be
written as:

$\displaystyle F_{m}$
$\displaystyle=\frac{\hat{\Gamma}_{m}^{\prime}z^{\prime}z\hat{\Gamma}_{m}}{d_{z}\hat{\sigma}^{2}_{e_{m}}},$
$\displaystyle=\frac{\hat{\tilde{\Delta}}_{m}^{\prime}\hat{\tilde{\Delta}}_{m}}{d_{z}\hat{\sigma}^{2}_{e_{m}}}$
$\displaystyle=\frac{n}{d_{z}}\frac{n^{-1}\sum_{i}\hat{\tilde{\Delta}}^{2}_{mi}}{\hat{\sigma}^{2}_{e_{m}}},$

for
$\hat{\sigma}^{2}_{e_{m}}=(p-z\hat{\Gamma}_{m})^{\prime}(p-z\hat{\Gamma}_{m})/(n-d_{z}-1)$.
Hence,

$\displaystyle
E[{\tilde{\Delta}}^{2}_{mi}]=plim(\frac{F}{n})d_{z}\sigma_{e_{m}}.$

###  7.8 Step 8 - Report Results

EXAMPLE BOX WITH MODELS, MCS P-VALUES, F STATISTICS, PICTURE OF DISTRIBUTION
OF PREDICTED MARKUPS, RSS?

##  8 Monte Carlo Evidence

We present in this section Monte Carlo evidence meant to illustrate the
performance of the testing procedures discussed previously. We start by
describing the setup for the simulation.

###  8.1 Setup

Simulation Model -  We generate data from a static model of demand and supply
in the class described in Section 2. The demand side follows the standard
mixed logit formulation. In market $t$, consumer $i$ chooses among
$\mathcal{J}_{t}=\\{1,...,J_{t}\\}$ products with characteristics
$(\mathbf{x}_{t},\mathbf{p}_{t})$ and for which consumer $i$ has an indirect
utility of the form

$U_{ijt}=\mathbf{x}_{jt}\beta+\mathbf{p}_{jt}\alpha+\bm{\xi}_{jt}+\bm{\mu}_{ijt}+\bm{\varepsilon}_{ijt}$
(51)

where $\bm{\xi}_{jt}$ is an unobserved product-market specific shock to
utility common to all consumers and $\bm{\mu}_{ijt}$ is an individual-specific
taste for product attributes given as:

$\mathbf{\mu}_{ijt}=\mathbf{x}_{jt}\mathbf{\upsilon}_{itx}\sigma_{x}+\mathbf{p}_{jt}\mathbf{\upsilon}_{itp}\sigma_{p}.$

where $\upsilon_{itx},\upsilon_{itp}\sim N(0,1)$. Finally, utility depends on
an idiosyncratic shock $\mathbf{\varepsilon}_{ijt}$ which is distributed iid
$T1EV$. The parameters governing consumer preferences are $\alpha$, $\beta$
and $\sigma$. For a given value of these parameters, the model implies a
matrix
$D_{\mathbf{p}_{t}}\equiv[\partial\mathbf{s}_{j}/\partial\mathbf{p}_{t}]$ of
partial derivatives of product $j^{\prime}$s market share with respect to
prices.

On the supply side we consider two candidate models of firm conduct that imply
markups $\mathbf{\Delta}_{m}$ in Equation (2): Nash-Bertrand price setting
$(B)$ and a collusive model in which firms maximize joint profits $(C)$. As in
Section 2, costs are assumed to be the sum of a linear index of the observed
cost shifters $\mathbf{w}$ and an unobserved component $\bm{\omega}$. For the
two models we consider, markups are respectively:

$\displaystyle\mathbf{\Delta}_{Bt}$ $\displaystyle=(\Omega_{Bt}\odot
D_{\mathbf{p}_{t}})^{-1}\mathbf{s}_{Bt}$ (52)
$\displaystyle\mathbf{\Delta}_{Ct}$ $\displaystyle=(\Omega_{Ct}\odot
D_{\mathbf{p}_{t}})^{-1}\mathbf{s}_{Ct},$ (53)

where $\Omega_{Bt}$ is the ownership matrix in market $t$ where element
$(i,j)$ is an indicator that the same firm produces products $i$ and $j$, and
$\Omega_{Ct}$ is a $\mathcal{J}_{t}\times\mathcal{J}_{t}$ matrix of ones.

Parametrization -  In our baseline, we have $N_{m}=200$ markets, $N_{f}=10$
firms and $N_{p}=40$ products. We first allocate all products to all markets,
and then randomly remove 40% of them, setting a higher probability of removing
products from lower market indices. Firm-product pairs are randomly drawn to
create an unbalanced ownership structure, where each firm can have at least 2
and at most 22 products. These allocation methods for product-market and firm-
product create significant variation in market structure, which is important
given the instruments that we use. The vector of product characteristics
$\mathbf{x}$ contains a constant and a scalar $\mathbf{x}^{(1)}$. The vector
of cost shifters $\mathbf{w}$ includes $\mathbf{x}$ and a scalar
$\mathbf{w}^{(1)}$. Both $\mathbf{x}^{(1)}$ and $\mathbf{w}^{(1)}$ are
independently drawn from a standard uniform distribution. In our baseline
specification we set the following parameter values:

Preference parameters:
$\displaystyle\qquad\sigma_{x}=3,\quad\sigma_{p}=0.25,\quad\alpha=-1.5,\quad\beta=(-6,6)$
Cost parameters: $\displaystyle\qquad\tau=(2,1,0.2)$ Unobserved shocks:
$\displaystyle\qquad(\bm{\xi}_{jt},\bm{\omega}_{jt})\sim
N(0,\Sigma),\quad\sigma^{2}_{\bm{\xi}}=\sigma^{2}_{\bm{\omega}}=0.2\text{ and
}\sigma_{\bm{\xi}\bm{\omega}}=0.$

Given parameter values, we draw observed $\mathbf{x}^{(1)}$,
$\mathbf{w}^{(1)}$, and unobserved shocks for each of the $N_{S}=100$
simulations and compute endogenous prices and quantities as the solution of
the market share equations and first order conditions for each model $m$. The
choice of parameter values and distributions create realistic outside shares
for the Bertrand DGP, around 0.9.

Instruments -  We construct two types of instruments for the Monte Carlo
exercise: BLP instruments and differentiation instruments. For product-market
$jt$, let $O_{jt}$ be the set of products other than $j$ sold by the firm that
produces $j$ and let $R_{jt}$ be the set of products produced by rival firms.
The instruments are:

$\mathbf{z}^{BLP}_{jt}=\left[\begin{matrix}\sum\limits_{k\in O_{jt}}1[k\in
O_{jt}]&\sum\limits_{k\in R_{jt}}1[k\in R_{jt}]&\sum\limits_{k\in
O_{jt}}\mathbf{x}_{k}&\sum\limits_{k\in
R_{jt}}\mathbf{x}_{k}\end{matrix}\right]$
$\mathbf{z}^{Diff}_{jt}=\left[\begin{matrix}\sum\limits_{k\in
O_{jt}}\mathbf{d}_{jkt}^{2}&\sum\limits_{k\in
R_{jt}}\mathbf{d}_{jkt}^{2}&\sum\limits_{k\in
O_{jt}}1[|\mathbf{d}_{jkt}|<sd(\mathbf{d})]&\sum\limits_{k\in
R_{jt}}1[|\mathbf{d}_{jkt}|<sd(\mathbf{d})]\end{matrix}\right]$

where, following gh19,
$\mathbf{d}_{jkt}\equiv\mathbf{x}^{(1)}_{kt}-\mathbf{x}^{(1)}_{jt}$ and
$sd(\mathbf{d})$ is the standard deviation across the distance vector. In most
of the exercises, we use differentiation instruments and exogenous cost-