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Causally motivated attribution for online advertising


Abstract and Figures

In many online advertising campaigns, multiple vendors, publishers or search engines (herein called channels) are contracted to serve advertisements to internet users on behalf of a client seeking specific types of conversion. In such campaigns, individual users are often served advertisements by more than one channel. The process of assigning conversion credit to the various channels is called "attribution," and is a subject of intense interest in the industry. This paper presents a causally motivated methodology for conversion attribution in online advertising campaigns. We discuss the need for the standardization of attribution measurement and offer three guiding principles to contribute to this standardization. Stemming from these principles, we position attribution as a causal estimation problem and then propose two approximation methods as alternatives for when the full causal estimation can not be done. These approximate methods derive from our causal approach and incorporate prior attribution work in cooperative game theory. We argue that in cases where causal assumptions are violated, these approximate methods can be interpreted as variable importance measures. Finally, we show examples of attribution measurement on several online advertising campaign data sets.
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Estimating The Effect Of Online Display Advertising On
Browser Conversion In Observational Data
Ori Stitelman
37 East 18th Street
New York, NY, 10003
Brian Dalessandro
37 East 18th Street
New York, NY, 10003
Claudia Perlich
37 East 18th Street
New York, NY, 10003
Foster Provost
NYU Stern School of Business
New York, NY, 10012
This paper examines ways to estimate the causal effect of
display advertising on browser post-view conversion (i.e. vis-
iting the site after viewing the ad rather than clicking on the
ad to get to the site). The effectiveness of online display ads
beyond simple click-through evaluation is not well estab-
lished in the literature. Are the high conversion rates seen
for subsets of browsers the result of choosing to display ads
to a group that has a naturally higher tendency to convert or
does the advertisement itself cause an additional lift? How
does showing an ad to different segments of the population
affect their tendencies to take a specific action, or convert?
We present an approach for assessing the effect of display ad-
vertising on customer conversion that does not require the
cumbersome and expensive setup of a controlled experiment,
but rather uses the observed events in a regular campaign
setting. Our general approach can be applied to many ad-
ditional types of causal questions in display advertising. In
this paper we show in-depth the results for one particular
campaign (a major fast food chain) of interest and mea-
sure the effect of advertising to particular sub-populations.
We show that advertising to individuals that were identi-
fied (using machine learning methods) as good prospective
new customers resulted in an additional 280 browsers visit-
ing the site per 100,000 advertisements shown. This result
was shown to be extremely significant. Whereas, displaying
ads to the general population, not including those that vis-
ited the site in the past, resulted in an additional 200 more
browsers visiting the site per 100,000 advertisements shown
(not significant at the ten percent level). We also show that
advertising to past converters resulted in a borderline sig-
nificant increase of an additional 400 browsers visiting the
site for every 100,000 online display ads shown.
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Categories and Subject Descriptors
H.2.8 [Database Management]: Database Applications—
data mining; I.2.6 [Artificial Intelligence]: Learning—in-
duction; I.5.1 [Pattern Recognition]: Models—statistics;
J.4 [Computer Applications]: Social and Behavioral Sci-
General Terms
Algorithms, Design, Experimentation
online display advertising, causal effects, predictive model-
ing, social networks, user-generated content, privacy
Controlled experiments, often called randomized tests or
A/B tests, are commonly used online to assess the effects
of any kind of changes to the browsing experience (formally
interventions) on browser behavior (see e.g.[6],[8],[7]). Some
of those efforts have been devoted to extending these ex-
periments to evaluating the causal effect of online display
advertising on browser conversion ([8],[7]). However, the
cost and difficulty of implementing A/B testing successfully
in the display ad environment are very high, as will be ex-
plained below. This makes analytical approaches that can
estimate the effect of ads while running the campaign reg-
ularly (observational setting; without creating any special
testing controls) appealing. Despite the appeal of estimat-
ing the effects based on observational data there are many
practical considerations that make this a difficult task. A
number of analytical methods have been developed in a wide
range of fields to estimate the causal effects of a binary treat-
ment on a binary outcome of interest. Much of the relevant
causal literature has been developed in the field of epidemi-
ology and biostatistics (see e.g. [15] and [23]). Though the
reasons for not using randomized tests in the medical liter-
ature are often different than in the advertising community,
the lessons learned from the use of causal methods there
are directly applicable to our current setting. For our pur-
poses the treatment of interest is an advertisement and the
outcome of interest is browser conversion such as visiting a
webpage of interest, providing an email address, or making
an online purchase. Ultimately, we are concerned with an-
swering the question: “What is the causal effect of online
display advertising?”
For the remainder of this article we will refer to A/B tests
as randomized tests. We will also interchangeably refer to
treatment as the act of showing an advertisement and refer
to a conversion or outcome of interest as taking a specific ac-
tion on the brand’s website. Furthermore, when we refer to
display advertising we mean online display advertising. We
will primarily focus in our experiments on whether or not
a browser visits the website (site visit) of the advertising
brand. We will also use the common convention that capi-
tal letters represent random variables and lower case letters
represent realizations of a level of those variables.
There are many difficulties of implementing A/B tests on-
line in general[5]. Kohavi, 2010, discusses the difficulties of
implementing a randomized test in the online setting and
provides examples of how the implementation of the ran-
domization test can result in unforeseen artifacts that make
estimating the intended effects difficult or impossible. In
fact, they suggest using a form of testing called A/A/B,
where there are three possible treatment scenarios–one for
the current treatment, another for the current treatment
using the A/B test implementation and a third for the new
treatment using the A/B test implementation. The A/A/B
test allows one to test if the observed effect is due to the
new treatment or due to the implementation of the test.
This type of set-up to assess the implementation of the test,
though sensible, begins to add new costs to the implementa-
tion that must be considered. A paper presented by Google
at the last KDD briefly addresses another major drawback
of implementing A/B tests for assessing the effect of dis-
play advertising on browser conversion[1]. The major con-
cern expressed was that advertisers would not want to pay
to present advertisements, such as public service announce-
ments (PSA), that did not promote their product. The fact
that A/B tests are prone to unforeseen error and that mar-
keters don’t want to pay to present PSAs, coupled with the
fact that there are additional overhead costs associated with
A/B testing, suggests that alternative methods for estimat-
ing causal effects without intervening on the observed system
would be preferable.
A common misconception is that randomized tests are the
only study design in which causal effects may be estimated
(see e.g.[6], [9]). In fact, there is a long history of litera-
ture devoted to estimating causal effects in observational,
or non-randomized, settings (see e.g. [18],[23],[20]). Rubin
[18] established a counterfactual framework that defines the
effect of all levels of possible treatment for each observed
subject, and allows for the consideration and estimation of
what would have happened when individuals received a spe-
cific level of treatment, possibly contrary to what is actually
observed. The outcomes for the unobserved levels of treat-
ment are referred to as potential outcomes in the literature.
This framework also allows one to define summary measures
that quantify the effect of the treatment on average for the
population or sub-population of interest. Two commonly re-
ported summary measures of interest include the difference
in the outcome probabilities and the ratio of the outcome
probabilities when treated versus not treated.
We will refer
These summary measures are typically referred to as addi-
"WHAT IF" Analysis
A/B Test
Show Ad
Conversion Rate
Conversion Rate
Saw Ad
See Ad
Saw Ad
Didn't See
& Estimator
Figure 1: Causal assumptions in the form of a causal
to the difference in conversion probabilities as the additive
impact of the advertisement, and the ratio as the relative
impact of the advertisement.
Chan et al., presented at last year’s KDD, proposed the
use of several related methods that are able to estimate the
effect of advertising in observational data[1]. In particular,
their paper focused on estimating the causal effect of ad-
vertising among those shown the advertisement, and high-
lighted the benefits of applying their methods in pipeline.
Several variants of the methods they surveyed as well as
others will be discussed below. In addition to implementing
variants of the methods they proposed, we will explore the
benefits of estimating several other parameters of interest,
explore another method for estimating causal effects (tar-
geted maximum likelihood estimation (TMLE))[24]), and
discuss some other advantages of estimating causal effects
beyond its implementation in pipeline. Furthermore, we
display the advantages of estimating causal effects within
different segments of the population.
Consider what is the purpose of implementing an A/B,
or randomized, test. The entire point of running the test is
to easily identify the effect of the treatment, or in our case
the display advertisement, on the outcome of interest. The
first step in a randomized study is to randomly assign each
subject, or browser, to one of two groups, A or B. The top
box in figure 1 shows this approach. The motivation for ran-
dom sampling is to ensure that both groups are similar with
respect to the distribution of all relevant variables that can
potentially affect the probability of taking the desired ac-
tion (e.g., gender, browsing activity, past purchase activity,
etc.). If the two groups were not similar, the difference in
the observed effect might be due to those variables and not
to the treatment. Variables that can affect both the proba-
bility of treatment and the probability of conversion would
tive or attributable risk and relative risk, respectively, in the
epidemiology and biostatistics literature because they were
commonly used to quantify the increase in the risk of a dis-
ease or death when exposed to a possibly harmful substance.
They define a pipeline as “an automated pipeline that re-
trieves data, computes estimates, and decides whether to
release results, suppress results, or send them to an expert
data analyst for review.”
make it difficult to estimate the effect of the treatment and
are known as confounders. Group A is then shown the ad-
vertisement and group B is not shown the advertisement.
Next the conversion rate is calculated for both groups and
is compared to assess the effect of showing the advertise-
ment. If the randomization is successful it allows one to
directly compare the outcomes of the two groups and the
practice of relying on it to make the conclusion about the
effect is known as the randomization assumption.
The bottom box in figure 1 outlines an approach for a
counterfactual analysis that allows the estimation of the ef-
fect directly in the observed data even in the presence of con-
founders. In observational data one cannot directly compare
the group that is shown the advertisement (the red rectan-
gle) to the group that is not shown the advertisement (the
gray rectangle) because of the confounding of targeting. The
group that was shown the ad was selected specifically because
they are assumed to have a higher conversion rate. There-
fore adjustment must be made for all variables that affect
the conversion rate. This is done by analytically conduct-
ing the counterfactual or “what if analysis. In general, the
approach is to use a model/estimator to estimate the con-
version rate had the entire population of interest been shown
the advertisement. Subsequently, the conversion rate is esti-
mated had the entire population not been shown the adver-
tisement and the two conversion rates are then compared. A
number of observational methods exist that provide a way
to adjust for the fact that the treated and untreated groups
are not the same with respect to the confounders in the ob-
served data. Several of these methods are discussed and
implemented in the subsequent sections.
In this paper we will describe a practical approach for es-
timating the causal effect of advertising. We will follow a
unified approach that may be extended to other interest-
ing causal questions of interest in the display advertising
environment. This approach relies on (1) posing the ques-
tion of interest (2) making assumptions about the observed
data (3) clearly identifying a parameter that answers the
question given the assumptions and (4) estimating the pa-
rameter. This approach loosely follows the roadmap for con-
structing a TMLE presented in [21]. However, rather than
just presenting a TMLE we will discuss several ways that
the parameter of interest may be estimated and expound on
the advantages and shortcomings of each method. Finally,
we will present an analysis of the effect of advertising for
a major fast food chain and use the presented methods to
assess the effect within different sub-populations of interest.
In summary our results show that advertising to past con-
verters, “re-targeting”, results in an additional 400 browsers
visiting the site for every 100,000 online display ads shown
(1.1 times more site visitors when shown the ad). Whereas,
advertising to individuals that were identified (using ma-
chine learning methods discussed in [14]) as good prospective
new customers results in a 1.5 times increase in conversions,
which equates to an additional 280 browsers visiting the site
per 100,000 advertisements shown (p-value < 10
). Fi-
nally, displaying ads to the general population, not including
those that visited the site in the past, resulted in 2.4 times
more site visits, or an additional 200 more browsers visiting
the site per 100,000 advertisements shown (p-value = .13).
Primarily we will focus on answering the question: “What
is the effect of display advertising on customer conversion?”
In particular, we are not just interested in the immediate
response of clicking. Increasingly, clicks are perceived as
notoriously random and unreliable measure of effectiveness
(see e.g. [2]). The much more relevant question is whether
seeing an ad (without necessarily clicking on it) affects the
probability of conversion (e.g., visiting the brand’s website)
within a reasonable timeframe (this is also known as a“post-
view” conversion). Answering this question for the universe
of all browsers may not be of great interest because that
population includes a large portion of people who are highly
unlikely to convert whether they are shown a particular ad-
vertisement or not. Moreover, the estimation problem is
potentially much more difficult when looking at the entire
population, rather than segments of the population, and
may require larger data sets to answer the question of inter-
est because of the low overall conversion rates. Fortunately,
the questions that have the most financial relevance from
the perspective of an advertiser relate to the effect of adver-
tising on appropriate populations that have higher baseline
conversion rates (even absent advertising) than the overall
population. We will focus on estimating how advertising af-
fects conversion, where conversion is measured in terms of
future site visits. We will focus on answering this question
for particular sub-populations of browsers. In particular, we
will focus on answering the following three questions:
1. What is the effect of display advertising on conversions
for individuals that have visited the site in the past?
2. What is the effect of display advertising on conversions
for potential new customers (browsers with no past
site-visits) that were targeted based on their natural
expected tendency to convert at a higher rate than the
general population?
3. What is the effect of display advertising on conversions
for potential new customers in the general population?
For illustrative purposes, we have chosen a campaign with
high conversion rates relative to other campaigns we have
analyzed. By doing this we are able to estimate parameters
that answer all three of these questions of interest reliably.
In cases where the conversion rates are low it may be difficult
to answer the third question of interest regardless of the
estimation method employed.
In this section we will define the data structure we use,
and introduce some notation as well as some overall causal
assumptions about the observed system. We will then use
those causal assumptions to define parameters of interest in
the following section.
Our data structure is a common one in the causal liter-
ature. For each subject i (i.e., browser) we observe O
, A
, Y
), where O
is an observation from the true, and
unknown, data generating distribution, P
A is the binary
random variable of intervention/treatment (i.e., showing an
ad), where A equals one if an individual is treated and zero
otherwise. W is a vector of baseline covariates that records
information specific to a browser prior to intervention. W
should in our case include the browser’s past web-activity,
The subscript 0 denotes truth, whereas a subscript n
will denote an estimate of the distribution.
Figure 2: Causal Graph
past actions taken, past advertisements viewed, as well as
any other relevant information that affects the outcome of
interest and the treatment level the browser is exposed to.
The random variable Y is the binary outcome of interest
(i.e., is equal to one when a browser takes the action of in-
terest and zero otherwise).
Now we can define a time ordering of the observed vari-
ables that allows us to factorize the data into an observed
data likelihood. The time ordering of the observed ran-
dom variables in this simple data structure corresponds to
a causal graph that implies a particular factorization of the
likelihood. The causal graph is shown in figure 2. More com-
plicated observed data structures require careful defining of
the time ordering of the variable and both time cues and
subject matter knowledge should be used in constructing a
causal graph. This causal graph lays out the assumptions
one is making that allow for the construction of a param-
eter of interest that directly answers the scientific or busi-
ness question of interest. Specifically, this causal structure
states that the baseline covariates are not caused by tar-
geting or conversion, and that targeting is not caused by
conversion. Furthermore, it states that there are no other
unobserved variables that cause both A and Y , or unob-
served confounders. Unobserved variables that cause any
of the nodes in the graph individually are okay. The fac-
torization of the likelihood that corresponds to our causal
assumptions is:
(O) =
z }| {
P (W )
(A,W )
z }| {
P (A | W )
(A,W )
z }| {
P (Y | A, W ) . (1)
Thus, the likelihood factorizes with a part associated with
the non-intervention nodes Q
= (Q
, Q
) and a factor
associated with the intervention node, g
. We refer to the
node for A as an intervention node because we are interested
in what happens to the outcome when we intervene on A,
showing an ad, for each browser.
The parameter of interest is specifically chosen to answer
our primary question, “What is the effect of display adver-
tising?” It is common in the machine learning community
to refer to “tuning parameters” such as “k” in the k-nearest
neighbor algorithm and the number of leafs in a regression
tree in general as parameters. This is not how we use the
term parameter here. In fact, when we define a parame-
ter of interest, we define a quantity of interest that directly
answers our question and thus we would like to obtain an es-
timate for it. This is a common use of the terms“parameter”
and “parameter estimation” in the statistics community.
Now that the likelihood of the observed data is factorized
according to a causal graph we can consider the interventions
(showing an ad) on the observed system and how one may
“observe”the outcome in the case of intervention A = a. The
counterfactual distribution of the data structure under inter-
vention is known by the causal inference community as the
G-computation formula[16]. The G-computation formula is
very similar to the do-calculus proposed by Pearl for causal
analysis[11]. The A node which we are intervening upon in
the causal graph is set to the intervention level, a, in the
likelihood and the conditional distribution of A given W is
removed from the likelihood since it is no longer a random
variable (it is now deterministically set by the intervention).
The following is the resulting G-computation formula, or
distribution of the data under intervention A = a:
(O) = P (W )P (Y | A = a, W ). (2)
The G-computation formula now may be used to guide the
choice of causal parameter that will be useful for answering
a particular business question of interest.
We are interested in the size of the effect of display adver-
tising. If we knew the true distributions Q
and Q
would we answer this question? One straightforward ap-
proach would be to evaluate the conditional distribution of
Y | A, W for A = 1 and then again for A = 0 at all possible
levels of baseline variables W . Then take the mean weighted
by P (W ) for each group. This would result in the two quan-
tities E
] and E
]. Where E
] is the
mean of Y assuming everyone in a population is treated
at level a. We can now combine E
] and E
in useful ways to assess the effect of different levels of the
treatment variable A. Two commonly used parameters of
this type are the following:
Additive Impact = Ψ
) = E
] E
Relative Impact = Ψ
) = E
] (4)
The additive impact quantifies the additive effect of show-
ing the advertisement to everyone in the population versus
not showing the ad to anybody in the population. This
value could be interpreted as the average number of addi-
tional conversions per 100 people had everyone been shown
the ad versus had everyone not been shown the ad. Thus, if
the additive impact were 3 percent the following statement
would be appropriate: “Showing the ad versus not showing
the ad results in 3 additional conversions per 100 browsers.”
The relative impact quantifies the multiplicative effect of the
advertisement. This quantity is the ratio of the probability
of the outcome had everyone been shown the ad divided by
the probability of the outcome had nobody been shown the
ad. Thus, a relative impact of 3 would correspond with the
following statement: “Showing the ad makes browsers on
average three times more likely to convert.” The choice of
parameter to estimate should be driven by the business ques-
tion one is trying to answer and in many situations it may be
useful to estimate both parameters. The additive impact di-
rectly addresses the return on investment while the relative
impact is highly influenced by the level of the untreated con-
version rate. If the untreated conversion rate is low a small
additive impact will manifest itself as a large relative impact
even-though the advertisment may have little affect on the
number of additional customers converting. One particular
advantage of using these parameters to answer our question,
rather than say log odds in a logistic regression, is that they
are numbers that may be interpreted by statisticians and
non-statisticians alike. Thus, the estimates may be handed
off to individuals with business knowledge to make action-
able decisions based on them.
Note that the parameters described above quantify the
effect of the advertisement over the entire population of in-
terest. Thus, any conclusions, or inferences, made from the
estimates generalize to the entire population being exam-
ined. For example, as we do below, we estimate the additive
impact of advertising among past site visitors for which a
medium size ad serving company received a bid request
Any inferences made based on an estimate are generalizable
to this group. This is a different parameter than the ones es-
timated by Google in their paper where they estimated the
effect only among the treated. Inferences made by the es-
timators and methodology proposed there are generalizable
only to a population that is treated[1]. Thus, the parameters
we propose to estimate here are generally valid for estimat-
ing the effect of advertising on a group of people to which
one could potentially advertise and who may or may not
have been advertised to in the past. This type of parameter
is directly relevant to answer business questions that regard
assessing the effect of potential interventions on the entire
group of browsers that may be intervened upon.
The process described in the preceding sections has been
primarily concerned with defining a parameter of interest
that directly answers the question: “What and how big is
the effect of display advertising?” The presented approach
loosely follows the first few steps of the unified approach pre-
sented in [21] for estimating causal effects. In this section we
explore alternative estimators that might be considered for
estimating the parameters defined in the previous sections.
Each of the estimators we will present is a function of an
estimate of the Q factor of the likelihood, the g factor of
the likelihood, or both. Up until now we have not presented
a model, or collection of possible data-generating distribu-
tions, for Q
, Q
, and g
. For Q
we will use the
empirical distribution, as this is the efficient non-parametric
maximum likelihood estimator for this distribution (It will
be explained later how this is done in practice). For the
two conditional distributions, Q
, and g
, ideally a non-
parametric model which imposes no rigid assumptions on the
functional form of the relationship would be used. However,
practical concerns given the size of the data and dimension-
ality of the problem make this a computationally difficult
task. So for the time being we employed a logistic regres-
sion model that performed cross-validated variable selection
for both main terms and polynomials of order 2 to estimate
the conditional distributions, Q
and g
. Note however,
that we are not interested in the estimated parameters of
this logistic model, but use it only to generally estimate
a functional dependence. One advantage of estimating the
functional dependence of the underlying distributions rather
A large percentage of the display advertising examined is
flowing through ad-exchanges with real-time bidding. When
a browser is visiting some site on the web, the site may send
a request to such an exchange including relevant information
on the browser. At that point, an auction is run in real-time
and the highest bidder gets to show the browser an ad. A bid
request is an event where the ad-exchange solicits potential
than one specific beta of a linear model is that as compu-
tation power increases, better methods with less bias can
come to bear that allow for searching over larger spaces.
Those methods can be incorporated directly into our pro-
cess for estimating causal effects. Thus, the better we get
at estimating conditional distributions, the better we get at
estimating causal effects. This is not the case for approaches
that pre-specify the causal effect as a specific parameter of
a linear regression or logistic regression model.
We will now present the different estimators ψ
of the
parameters of interest Ψ shown above. We refer the reader
to external sources for more in-depth understanding of each
estimator, as that is outside the scope of this paper.
each of them, we will define the estimator as well as de-
scribe some characteristics and develop intuition about when
the estimator behaves well and when it may break down in
practice. The estimators under consideration are unadjusted
(UNADJ), a maximum-likelihood based evaluation of the g-
computation parameter (MLE), inverse treatment weighted
(IPTW), augmented-IPTW (AIPTW), and targeted maxi-
mum likelihood (TMLE). For a more in-depth treatment of
these estimators see [4].
For each estimator, or method, we will estimate the aver-
age conversion rate for everyone as though they were shown
the advertisement, ψ
, and for everyone as though
they were all not shown the advertisement, ψ
These estimates then may be combined to estimate the ad-
ditive impact (AI) and relative impact (RI) in the following
= ψ
= ψ
We will now begin to describe the different methods of
estimation. The unadjusted estimate (UNADJ) is a biased
estimate of the causal effect because it does not account for
the fact that individuals who are more likely to get adver-
tised to are also more likely to convert. In other words,
the estimator does not account for confounding. The UN-
ADJ estimator for relative risk is the conversion rate of the
treated divided by the conversion rate of the untreated. Sim-
ilarly, the UNADJ estimator for the additive impact is the
conversion rate of the treated minus the conversion rate of
the untreated:
= a)Y
= a)
. (7)
An MLE based estimator is a substitution estimator that
relies on a consistent estimate of the conditional distribution
. By a substitution estimator, we are specifically refer-
ring to the fact that the estimator follows the proper bounds
of the model (i.e., estimates probabilities between 0 and 1)
by evaluating at a particular P
. It takes the following form:
(a, W
). (8)
Some drawbacks of this method are that there is no available
theory for the construction of the variance estimates and
The subscript n indicates this to be an estimate (rather
than truth) based on n observations.
therefore confidence intervals. Furthermore, it is not robust
to mis-specification of the outcome regression model.
The IPTW estimator is an estimating equation-based es-
timator that adjusts for confounding through g. Thus, it is
a consistent estimate of the causal effect when g
is a con-
sistent estimate of g
. Unlike a substitution estimator, the
estimating equation estimators do not obey the bounds of
the proper model (i.e. return estimates of probabilities not
between 0 and 1). The estimator takes the following form:
n,IP T W
= a)Y
, W
. (9)
The A-IPTW estimator is an estimating equation-based
estimator that is doubly robust. Double robustness means
that it is a consistent estimate of the causal effect when ei-
ther Q
is a consistent estimate of Q
or g
is a consistent
estimate of g
. Furthermore, the A-IPTW estimator is lo-
cally efficient. The A-IPTW estimator is:
= a)
, W
(a, W
(a, W
Both the IPTW estimator and the A-IPTW estimator may
blow up when g
, W
) is not well-bounded. In situa-
tions where g
, W
) is close to zero for some of the ob-
served browsers these estimators may be unstable. A quick
examination of these estimators reveals why they may be
unstable. Since g
, W
) is in the denominator if it is
close to zero it will result in a very large contribution to the
estimating equation for the particular browser. This contri-
bution is unbounded when g
, W
) is not bounded and
this can end up resulting in a very poor estimate. The lack
of boundedness of g
, W
) has been called a violation of
the positivity assumptions or an ETA (experimental treat-
ment assumption). For a more thorough discussion of these
types of violations see [12],[15],[17].
The last estimator we will explore is the Targeted Max-
imum Likelihood Estimator (TMLE). TMLE is a substitu-
tion estimator, like MLE above. Moreover, the TMLE is
double robust and locally efficient [10], like A-IPTW. The
), is of the following form:
(a, W
), (11)
where Q
(a, W
) is an update of Q
(a, W
) specifically
chosen to target the parameter of interest. This update is
done by fluctuating Q
(a, W
) with a parametric sub-model
of the following form:
(a, W
)) = logit(Q
(a, W
) + h
, W
)), (12)
where h
, W
) = I(A
= a)/g
(a, W
). Using the
logit here is just a computational trick to arrive at the TMLE
and is not based on the fact that logistic regression was used
to estimate the initial Q
or g
. Implementing this sub-
model fluctuation can easily be done using the standard glm
function in most statistical packages with an offset equal to
the inverse logit of Q
(a, W
). The theoretical basis for
the choice of h(A, W ) is explained in van der Laan’s semi-
nal paper on TMLE [25]. A more in-depth explanation of
the implementation, as well as code for implementing this
TMLE may be found in Gruber and van der Laan’s gentle
introduction to TMLE[3]. The TMLE is not as sensitive to
violations in the positivity assumption as the A-IPTW and
IPTW estimators presented above because the contribution
of each browser to the estimator is bounded between 0 and 1.
Thus, the estimator follows a proper model and the final es-
timates are guaranteed to produce a proper probability that
falls in the expected range. However, under more extreme
violations of the positivity assumption, the TMLE may also
lose some stability and extensions of TMLE that are more
robust in these situations have been proposed and imple-
mented [22, 4, 19]. These methods are outside the scope of
the current paper.
Confidence intervals and p-values for the A-IPTW, and
TMLE may be constructed using the variance of the influ-
ence curve as described in [3]. They can be similarly con-
structed for the IPTW estimator; however, they should be
conservative for the IPTW estimator. Alternatively, boot-
strap methods may be used to construct these estimates and
have been shown to construct better estimates of confidence
intervals in finite samples (see e.g [19]).
In this paper we focused on estimating the effect of dis-
play advertising for one marketer of interest. The marketing
campaign analyzed was for a major fast food chain. Each of
the above methods was implemented to estimate the effect
of advertising in each of the following three sub-populations:
1. Individuals who have visited the chains website in the
past, or Action Takers (AT).
2. Individuals who have not visited the site in the past
but were targeted based on their natural tendency to
convert at a higher rate than the general population,
or Network Neighbors (NN). These individuals were
targeted using machine learning algorithms.
3. Individuals who have not visited the site, or Run-of-
Network (RON).
In each case the data was sampled in the following way:
1. A day t
was defined
2. On t
all individuals within the specified sub-population
for whom a medium-sized ad serving company received
a bid request were sampled.
3. W , the vector of potential confounders at baseline,
was recorded. These potential confounders included
past browsing content, past browsing intensity, IP type
(.com, .org, .gov, etc.), Internet connection type, browser
used, number of times an ad network has seen the
browser, and days since the browser was first seen, as
well as if an individual visited the site in the past two
4. On the following day, t
+ 1, it was recorded whether
each sampled browser saw an advertisement for the
marketer of interest. A = 1 for individuals who saw an
advertisement for the marketer. It was also recorded
whether or not the individual took the desired action
between t
and the time of the impression. If an in-
dividual took an action prior to seeing the impression,
this action was recorded in their vector of baseline vari-
ables, W.
5. The action window was determined to be five days.
6. For those shown the advertisemen,t the action window
begins the second the first advertisement is shown on
+ 1. For those not shown the advertisement, the
action window starts at the same time of day on t
+ 1
that the first bid request is observed on t
7. Each browser was observed for the following five days
in seconds and the second the five day window closes it
was recorded if the action was observed in the action
window. If an action was observed Y = 1 and if no
action was observed Y = 0.
Since the data was sampled in this way the causal effects
estimated may be used to make inferences about how adver-
tising affects conversions in the sub-population(e.g. past site
visitors) for whom the ad company received bid requests.
Choosing the time to start the action window for the un-
treated, A = 0, requires some assumptions since there is no
action, such as an advertisement, for which to start the ac-
tion window. Fortunately, since this is for the unadvertised
group there is no reason to believe that right after the start
of the window there should be a jump in the probability of
converting right at that time. Thus, we chose to use time
of day on t
+ 1 that the first bid request was observed on
. We did a sensitivity analysis and chose other points in
time to start the action window and no difference was seen
in the results. It should be made completely clear that the
action window was still exactly 5 days to the millisecond for
both those shown the advertisement and those not shown
the advertisement.
Table 1 shows the results of our experiments using the
approaches described in the previous sections. In particu-
lar, for each of the 5 methods we show the estimates of the
conversion rates (C-Rates) with and without the ad as well
as the measures of impact. The p-values of 0.000 in the
table indicate that the p-value was less than 10
. The
p-value is not shown for the UNADJ estimates since those
estimates are known to be biased, and thus the p-values do
not provide relevant information. The p-values for the MLE
estimate are not provided since there are no theoretical ba-
sis for their construction as discussed above. The p-values
are displayed for the additive impact and the p-values for
relative impact are similar.
In order to obtain reasonable results for the IPTW and
AIPTW estimators, the estimated treatment probabilities
had to be bounded at .98. Thus, all predictions g
(a =
1, W
) that were greater than 0.98 were set to 0.98. The
results without this truncation are shown in Table 2. The
violation in the positivity assumption has a drastic effect
on the estimate of the conversion probability for the un-
treated. This is because there are levels of baseline vari-
ables that are almost perfectly predictive of being shown
an ad, and the IPTW and AIPTW estimator contributions
for those browsers is extremely high, as discussed above,
causing the estimate to fall way outside the range of a prob-
ability, between 0% and 100%. While these observations
have sufficient influence in the situation presented in table
2 to drive the estimate out of the proper range, it is also
possible that less severe violations can bias the results even
No Ad C-Rate 3.6% 3.6% 15.4% 9.6% 3.7%
Ad C-Rate 4.4% 4.1% 4.1% 4.2% 4.1%
Relative Impact 1.2 1.1 0.3 0.4 1.1
Additive Impact 0.8% 0.5% -11.4% -5.5% 0.4%
p-value 0.17 0.48 0.05
No Ad C-Rate 0.51% 0.52% 0.52% 0.51% 0.52%
Ad C-Rate 1.03% 0.73% 0.81% 0.83% 0.80%
Relative Impact 2.0 1.4 1.5 1.6 1.5
Additive Impact 0.52% 0.21% 0.29% 0.33% 0.28%
p-value 0.000 0.000 0.000
No Ad C-Rate 0.15% 0.15% 0.15% 0.15% 0.15%
Ad C-Rate 0.37% 0.37% 0.35% 0.37% 0.35%
Relative Impact 2.5 2.5 2.4 2.5 2.4
Additive Impact 0.23% 0.23% 0.20% 0.22% 0.20%
p-value 0.126 0.097 0.125
Table 1: Conversion Rates and Impact Of Advertis-
ing for the three different subpopulations.
if the estimates are within the proper range. For this rea-
son the TMLE is preferable. Situations where the IPTW
and A-IPTW estimators blow up and the TMLEs are stable
are fairly common and not specific to the situation observed
here. In fact, there are many articles that address this is-
sue (see e.g., [13],[22],[19]). Notice in Table 1 even after
bounding the denominator g
, though the resulting IPTW
and A-IPTW point estimates lie in the appropriate range
for the ATs, they are still returning unreasonable (biased)
results. In fact the point estimate for IPTW suggests that
displaying the advertisement results in 11,400 less conver-
sions per every 100,000 times the display advertisement is
shown, and the A-IPTW estimate 5,500 less conversions per
100,000. The fact that certain individuals are targeted for
ads based on their characteristics suggests that violations in
the positivity assumption are common in the display adver-
tising environment, making the instability of the IPTW and
A-IPTW a valid concern.
No Ad C-Rate 136.3% -119901.8% 3.6%
Ad C-Rate 4.1% 4.2% 4.2%
Table 2: Impact Of Advertising To Past Converters
With Unbounded g
Causes IPTW and A-IPTW
Estimates To Blow Up
Now we will make some general observations based on Ta-
ble 1 presented above. For these observations, we will focus
on the results based on the TMLE. For past action takers,
AT, the advertisement results in 400 extra conversions for
every 100,000 times the advertisement was displayed. How-
ever, this difference is only borderline significant, suggesting
that there may or may not be an effect of showing the ad-
vertisement to past action takers. It is not particularly sur-
prising that the effect is borderline significant considering
that the act of retargeting, or displaying the advertisement
to people that have visited the site in the past, is a common
practice in display advertising. The untreated, or those not
exposed to the advertisement in the AT segment of the pop-
ulation, most probably have been shown the display adver-
tisement several times by other firms that perform display
advertising. For network neighbors, NN, if all of them were
shown an advertisement 800 people out of 100,000 would
have converted; whereas, if they were all not shown an ad-
vertisement 520 would have converted. The advertisement
results in an extra 280 conversions for every 100,000 times
the advertisement was displayed or a 1.5 times greater con-
version rate. This difference in the conversion rates is ex-
tremely significant with a p-value of less than 10
. For
run-of-network, RON, if all of them were shown an adver-
tisement 350 people out of 100,000 would have converted;
whereas, if they were all not shown an advertisement 150
would have converted. The advertisement results, within
RON, in an extra 200 conversions for every 100,000 times
the advertisement was displayed or a 2.4 times greater con-
version rate. (Note that ratios may be different than just di-
viding treated by untreated probabilities that are displayed
because of rounding.) The effect of the advertisement within
RON is not significant at the 10 percent level.
Now for some general observations comparing the effects
of advertising between sub-groups. The base conversion
rates for ATs are much larger than for NNs. Unexposed
ATs provide 3,180 more conversions than unexposed NNs
per 100,000 browsers. In addition, the base rate (unexposed)
for RON is 150 conversions per 100,000 browsers while the
base rate for NNs is 520. This suggests that the machine
learning algorithm mechanism used for choosing individu-
als to target is successfully choosing individuals that have
higher base conversion rates than RON. In fact, those peo-
ple grouped into the NN segments are 3.5 times more likely
than RON to convert even when not shown the advertise-
ment. Furthermore, the effect of advertising to the NNs
is larger than the effect of advertising to RON, 280 extra
conversions per 100,000 advertisements shown versus 200.
This suggests that the machine learning algorithms used to
choose individuals to target for display advertisements based
on their propensity to convert are successfully choosing in-
dividuals that are more likely to respond to the display ad-
In this section we will present some evidence that the
methods presented above are actually performing as expected.
There are several simulations studies for TMLE that display
how it performs under different scenarios and compare its
performance to the other methods presented above (see e.g.
[13], [22],[10] ). We will present here some additional analy-
ses that verify that the methods are working in our current
First a negative test was performed. In this test we ana-
lyzed whether the advertisement for a different marketer, a
telecommunications company, had any effect on the conver-
sions for the fast food chain we were analyzing above. By
performing this test, we can see if the methods we have im-
plemented are returning spurious results when, in fact, there
is no effect of the advertisement. In running this test we
would expect the telecommunication company’s advertise-
ment to have no effect on the fast food site visit conversions.
For comparison between sub-groups that have different un-
treated conversion rates we prefer comparing based on addi-
tive impact since relative impact is highly influenced by the
level of the untreated conversion rate as discussed above.
Table 3 presents the results of this test for the marketer of
interest’s ATs. The TMLE estimates that browsers shown
the advertisement will convert at a rate of 3.79 percent and
those not shown the advertisement convert at a rate of 3.84
percent for an additive difference of -0.06 percent (p-value
0.89). Thus no effect of the telecommunication company’s
ad was observed.
No Ad C-Rate 3.84% 3.85% 3.89% 3.84% 3.84%
Ad C-Rate 4.07% 3.59% 3.89% 3.79% 3.79%
Relative Impact 1.06 0.93 1.00 0.99 0.98
Additive Impact 0.23% -0.26% -0.00% -0.05% -0.06%
p-value .99 0.91 0.89
Table 3: Impact Of Telecommunication Company’s
Advertisement On Fast Food Conversion
Another test we ran to assess the validity of our proposed
approach is that we compared the results to an A/B test that
was recently run. The test was run for a different market-
ing campaign of a clothing retailer. The A/B test revealed a
conversion rate for showing the advertisement of 3.26 conver-
sions per 1,000 people compared to a TMLE estimate of 3.19
conversions per 1,000 people. For the untreated, the A/B
test estimate was 9.9 conversions per 10,000 compared to 8.2
conversions per 10,000. Again, the IPTW and EE equation-
based methods did not perform as well as the TMLE. For the
untreated estimates, they were close; however, both meth-
ods estimated 2.2 conversions per 1,000 people for showing
the advertisement.
The results displayed above show that by using methods
developed in other fields for estimating causal effects, we can
estimate the effect of advertising in observational data and
alleviate the need for implementing an A/B, or randomized,
test. These methods may also be used to estimate the ef-
fect of the advertisement within particular sub-populations
of interest. We showed that for a particular fast food mar-
keting campaign the display advertisement resulted in an
additional 280 extra conversions per 100,000 non-past ac-
tion takers that were targeted for advertising (NNs), and 200
additional conversions for run-of-network (RON). The effect
estimated within the NNs is extremely significant while the
effect within RON is not significant at the 10 percent level.
We also showed that advertising to past action takers results
in borderline significant increase of 400 extra conversions per
every 100,000 times the advertisement is displayed. Despite
the fact that the estimated additive impact for ATs is higher
than for NNs (400 vs. 280), those conversions for non past
action takers (NNs and RON) are potentially more valuable
from the company’s perspective because they represent a
new stream of potential income, and once they convert they
become ATs.
The above results also displayed the stability and robust-
ness of using a double robust substitution estimator, tar-
geted maximum likelihood estimation (TMLE), to estimate
the causal effect of advertising. Inverse probability weighted
estimators (IPTW) and estimating-equation based double
robust estimators (A-IPTW) tend to be unstable when es-
timating the causal effect of advertising in situations where
there are levels of baseline variables that are highly predic-
tive of browsers seeing a particular display ad in the sub-
population of interest. The stability of TMLE relative to
these other methods, in these situations where the positiv-
ity assumption is violated, makes it particularly appealing
for estimating the causal effect of online display advertising.
The analysis presented here is just one example of how
causal effect estimation methods may be implemented in the
display advertising environment. Extensions of the approach
presented here may be used to answer other causal business
questions of interest. For example, the approach presented
may be used to estimate the effect of the intensity of display
advertising, the timing of display advertising, or the creative
being displayed. Furthermore, extensions of these methods
may be used to estimate the effect of advertising on the time
until customer conversion.
We would like to thank Tom Phillips, Rod Hook, Brian
May, and Andre Comeau for their valuable insights and sug-
gestions. We would also like to thank Edward Capriolo,
whose patience and support in using the Hadoop distributed
file system and HIVE query language was critical, and with-
out whom this analysis would not have been possible.
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... Marketers seek and prefer solutions that allow the creation of daily reports which are based on day-to-day budget management (Shao & Li, 2011). Dalessandro et al. (2012) state that proper conversion attribution models must be: • fair-all channels must be taken under consideration and show a proper impact on the fi nal conversion, • data-driven-a valuable conversion attribution model should be designed for advertising campaign goals and assess both consumer reaction to advertisements and data on conversions from the campaign, • interpretable-it should be widely accepted by practitioners involved in the marketing industry; acceptance should arise on the basis of the gained metrics and an intuitive understanding of model rules. Danaher and van Heerde (2018) distinguish fi ve elements of a good attribution model: • increases the marginal eff ect of a particular medium on purchase probability; • equals to zero when the medium produces no eff ect; ...
... • Is there any simplifi ed method to involve the eff ects of earned and category media without having a complete view on the entire customer journey? (as proposed by Dalessandro et al. (2012) for display advertising without experiments and extended data sets) • What is the impact of touchpoints coming from particular OPEC model areas on customer experience, loyalty, customer lifetime value? • Does the quality of the content faced by customers in earned media and category media signifi cantly infl uence fi nal purchase? ...
Full-text available
Marketers are currently focused on proper budget allocation to maximize ROI from online advertising. They use conversion attribution models assessing the impact of specific media channels (display, search engine ads, social media, etc.). Marketers use the data gathered from paid, owned, and earned media and do not take into consideration customer activities in category media, which are covered by the OPEC (owned, paid, earned, category) media model that the author of this paper proposes. The aim of this article is to provide a comprehensive review of the scientific literature related to the topic of marketing attribution for the period of 2010-2019 and to present the theoretical implications of not including the data from category media in marketers' analyses of conversion attribution. The results of the review and the analysis provide information about the development of the subject, the popularity of particular conversion attribution models, the ideas of how to overcome obstacles that result from data being absent from analyses. Also, a direction for further research on online consumer behavior is presented.
... through different channels. Similarly, Dalessandro et al. (2012) address the need of having methods that provide causal inferences and propose a method to alleviate endogeneity in the estimation. ...
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The integration of technology in business strategy increases the complexity of marketing communications and urges the need for advanced marketing performance analytics. Rapid advancements in marketing attribution methods created gaps in the systematic description of the methods and explanation of their capabilities. This paper contrasts theoretically elaborated facilitators and the capabilities of data-driven analytics against the empirically identified classes of marketing attribution. It proposes a novel taxonomy, which serves as a tool for systematic naming and describing marketing attribution methods. The findings allow to reflect on the contemporary attribution methods’ capabilities to account for the specifics of the customer journey, thereby, creating currently lacking theoretical backbone for advancing the accuracy of value attribution.
The statistics profession is at a unique point in history. The need for valid statistical tools is greater than ever; data sets are massive, often measuring hundreds of thousands of measurements for a single subject. The field is ready to move towards clear objective benchmarks under which tools can be evaluated. Targeted learning allows (1) the full generalization and utilization of cross-validation as an estimator selection tool so that the subjective choices made by humans are now made by the machine, and (2) targeting the fitting of the probability distribution of the data toward the target parameter representing the scientific question of interest. This book is aimed at both statisticians and applied researchers interested in causal inference and general effect estimation for observational and experimental data. Part I is an accessible introduction to super learning and the targeted maximum likelihood estimator, including related concepts necessary to understand and apply these methods. Parts II-IX handle complex data structures and topics applied researchers will immediately recognize from their own research, including time-to-event outcomes, direct and indirect effects, positivity violations, case-control studies, censored data, longitudinal data, and genomic studies. "Targeted Learning, by Mark J. van der Laan and Sherri Rose, fills a much needed gap in statistical and causal inference. It protects us from wasting computational, analytical, and data resources on irrelevant aspects of a problem and teaches us how to focus on what is relevant – answering questions that researchers truly care about." -Judea Pearl, Computer Science Department, University of California, Los Angeles "In summary, this book should be on the shelf of every investigator who conducts observational research and randomized controlled trials. The concepts and methodology are foundational for causal inference and at the same time stay true to what the data at hand can say about the questions that motivate their collection." -Ira B. Tager, Division of Epidemiology, University of California, Berkeley
Written by one of the preeminent researchers in the field, this book provides a comprehensive exposition of modern analysis of causation. It shows how causality has grown from a nebulous concept into a mathematical theory with significant applications in the fields of statistics, artificial intelligence, economics, philosophy, cognitive science, and the health and social sciences. Judea Pearl presents and unifies the probabilistic, manipulative, counterfactual, and structural approaches to causation and devises simple mathematical tools for studying the relationships between causal connections and statistical associations. The book will open the way for including causal analysis in the standard curricula of statistics, artificial intelligence, business, epidemiology, social sciences, and economics. Students in these fields will find natural models, simple inferential procedures, and precise mathematical definitions of causal concepts that traditional texts have evaded or made unduly complicated. The first edition of Causality has led to a paradigmatic change in the way that causality is treated in statistics, philosophy, computer science, social science, and economics. Cited in more than 5,000 scientific publications, it continues to liberate scientists from the traditional molds of statistical thinking. In this revised edition, Judea Pearl elucidates thorny issues, answers readers’ questions, and offers a panoramic view of recent advances in this field of research. Causality will be of interests to students and professionals in a wide variety of fields. Anyone who wishes to elucidate meaningful relationships from data, predict effects of actions and policies, assess explanations of reported events, or form theories of causal understanding and causal speech will find this book stimulating and invaluable.
This paper examines ways to estimate the causal effect of display advertising on browser post-view conversion (i.e. vis-iting the site after viewing the ad rather than clicking on the ad to get to the site). The effectiveness of online display ads beyond simple click-through evaluation is not well estab-lished in the literature. Are the high conversion rates seen for subsets of browsers the result of choosing to display ads to a group that has a naturally higher tendency to convert or does the advertisement itself cause an additional lift? How does showing an ad to different segments of the population affect their tendencies to take a specific action, or convert? We present an approach for assessing the effect of display ad-vertising on customer conversion that does not require the cumbersome and expensive setup of a controlled experiment, but rather uses the observed events in a regular campaign setting. Our general approach can be applied to many ad-ditional types of causal questions in display advertising. In this paper we show in-depth the results for one particular campaign (a major fast food chain) of interest and mea-sure the effect of advertising to particular sub-populations. We show that advertising to individuals that were identi-fied (using machine learning methods) as good prospective new customers resulted in an additional 280 browsers visit-ing the site per 100,000 advertisements shown. This result was shown to be extremely significant. Whereas, displaying ads to the general population, not including those that vis-ited the site in the past, resulted in an additional 200 more browsers visiting the site per 100,000 advertisements shown (not significant at the ten percent level). We also show that advertising to past converters resulted in a borderline sig-nificant increase of an additional 400 browsers visiting the site for every 100,000 online display ads shown.
Random forests are a combination of tree predictors such that each tree depends on the values of a random vector sampled independently and with the same distribution for all trees in the forest. The generalization error for forests converges a.s. to a limit as the number of trees in the forest becomes large. The generalization error of a forest of tree classifiers depends on the strength of the individual trees in the forest and the correlation between them. Using a random selection of features to split each node yields error rates that compare favorably to Adaboost (Y. Freund & R. Schapire, Machine Learning: Proceedings of the Thirteenth International conference, ***, 148–156), but are more robust with respect to noise. Internal estimates monitor error, strength, and correlation and these are used to show the response to increasing the number of features used in the splitting. Internal estimates are also used to measure variable importance. These ideas are also applicable to regression.
In observational cohort mortality studies with prolonged periods of exposure to the agent under study, it is not uncommon for risk factors for death to be determinants of subsequent exposure. For instance, in occupational mortality studies date of termination of employment is both a determinant of future exposure (since terminated individuals receive no further exposure) and an independent risk factor for death (since disabled individuals tend to leave employment). When current risk factor status determines subsequent exposure and is determined by previous exposure, standard analyses that estimate age-specific mortality rates as a function of cumulative exposure may underestimate the true effect of exposure on mortality whether or not one adjusts for the risk factor in the analysis. This observation raises the question, which if any population parameters can be given a causal interpretation in observational mortality studies?In answer, we offer a graphical approach to the identification and computation of causal parameters in mortality studies with sustained exposure periods. This approach is shown to be equivalent to an approach in which the observational study is identified with a hypothetical double-blind randomized trial in which data on each subject's assigned treatment protocol has been erased from the data file. Causal inferences can then be made by comparing mortality as a function of treatment protocol, since, in a double-blind randomized trial missing data on treatment protocol, the association of mortality with treatment protocol can still be estimated.We reanalyze the mortality experience of a cohort of arsenic-exposed copper smelter workers with our method and compare our results with those obtained using standard methods. We find an adverse effect of arsenic exposure on all-cause and lung cancer mortality which standard methods fail to detect.