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Are Physicians ‘Easy Marks’?: Quantifying the Effects of Detailing and
Sampling on New Prescriptions
by Natalie Mizik
Columbia University Robert Jacobson
University of Washington
ISBM Report 9-2003
Institute for the Study of Business Markets The Pennsylvania State University
402 Business Administration Building University Park, PA 16802-3004
(814) 863-2782 or (814) 863-0413 Fax www.isbm.org [email protected]
Are Physicians ‘Easy Marks’?: Quantifying the Effects of Detailing and Sampling on New Prescriptions§
Natalie Mizik* Columbia University
Graduate School of Business 3022 Broadway, Uris Hall, Room 513
New York, NY 10027-6902 Tel: 212-854-9818 Fax: 212-854-7647
e-mail: nm2079@ columbia.edu
Robert Jacobson Evert McCabe Distinguished Professor of Marketing
University of Washington School of Business
Box 353200 Seattle, WA 98195-3200
Tel: 206-543-4780 Fax: 206-685-9392
e-mail: [email protected]
October 2003
__________________________________________ § Data used in this study were made available to us by a US pharmaceutical manufacturer with the only condition of ensuring the confidentiality of the company and the specific drugs in the study. The authors received no financial support for this research from either the original data provider, or any other member of the pharmaceutical industry, or any of the syndicated data providers. We gratefully acknowledge a 2001 ISBM Business Marketing Doctoral Student Support Award Competition research grant from the Institute for the Study of Business Markets (ISBM) at Pennsylvania State University. * Corresponding author
Abstract
While much public attention and considerable controversy surround pharmaceutical
marketing practices and their impact on physicians, views on the matter have largely been shaped by
anecdotal evidence or results from analyses with insufficient controls. Making use of a dynamic
fixed effects distributed lag regression model, we empirically assess the role that two central
components of pharmaceutical marketing practices (namely, detailing and sampling) have on
physician prescribing behavior. Key differentiating features of our model include its ability to (i)
capture persistence in the prescribing process and decompose it into own-growth and competitive-
stealing effects, (ii) estimate an unrestricted decay structure of the promotional effects over time, and
(iii) control for physician-specific effects which, if not taken into account, induce biased coefficient
estimates of detailing and sampling effects. Based on pooled time series cross-sectional data
involving 3 drugs, 24 monthly observations and 74,075 individual physicians (over 2 million
observations in total), we find that detailing and free drug samples have positive and statistically
significant effects on the number of new prescriptions issued by a physician. However, contrary to
the dominant views in the public policy debate and the results of earlier studies, we find that the
magnitudes of the effects range from modest to very small. Rather than being “easy marks,” our
findings are consistent with physicians being “tough sells.”
1
As the cost of prescription drugs continues to escalate, considerable attention is being
focused on the interactions between pharmaceutical sales representatives (PSRs) and physicians as
one source of the problem. Concern that pharmaceutical marketing practices have exacerbated
increases in prescription drug costs prompted the US federal government to issue a recent warning to
the drug industry to curtail some of their practices (The Washington Post, October 2, 2002). A
number of states have undertaken “counter-detailing” initiatives where state employees visit
physicians in hopes of persuading them to switch to prescribing lower cost generic drugs (Wall Street
Journal, August 22, 2001).
The US pharmaceutical industry is estimated to spend $4.7 billion on detailing, i.e., PSRs
visiting physicians to promote their firm’s drugs (IMS Health, April 1, 2002). Further, the retail value
of the free drug samples distributed during these visits is estimated at $10 billion. A typical PSR
visit lasts 2-5 minutes where a PSR discusses one to three of the company’s drugs. Information (and,
at times, misinformation) about a drug’s composition, therapeutic value, proper dosage, and potential
side effects is communicated (Zigler, Lew, and Singer 1995). Oftentimes PSRs will also provide
information about retail price, dispense samples, and possibly offer small gifts to the physician.
Claims that these interactions with PSRs compromise physician integrity and affect
prescribing behavior elicit heated debate. Two competing views have dominated discussion on the
matter. The prevailing view contends that PSRs significantly influence physicians’ prescribing
behavior and that his influence has negative effect on patients’ welfare in that PSRs encourage the
physicians to prescribe more expensive branded drugs. Many public policy organizations and
consumer advocacy groups adhere to this view. Waud (2000), for example, states: “I have seen no
evidence that the friendly detail man adds anything positive. I have heard anecdotes about
occasional pearls passed on by detail men, but generally, the “education” is a thinly disguised selling
job. And they are good at it.” The Los Angeles Times (October 16, 2000) quotes a Blue Cross of
California spokesperson’s assertion that: “So much of what physicians learn about drugs comes from
2
the weekly visits of the Kens and Barbies… They shower doctors with free drug samples, in part to
encourage them to prescribe the product.”
A prominent alternative view argues that PSRs do influence physicians’ prescribing behavior,
but this influence is positive in that PSRs provide physicians with valuable information. As a result,
physicians are better informed and make better choices for their patients. Pharmaceutical companies
and industry groups advocate this view. Spilker (2002), for example, argues that the role of the sales
representative is educational and that they “perform valuable functions that promote better patient
care.” Specifically they allow doctors to stay up to date on new treatments, new approved uses for
existing medicines, contraindications, new dosages, drug interactions, and new ways to monitor the
patients. Under this view, detailing is generally depicted as a mechanism for speeding up the
adoption of new and better treatments, which leads to better patient outcomes.
Despite the substantial resources pharmaceutical companies invest in promoting their
products and the controversy associated with pharmaceutical marketing practices, surprisingly little
is known about the impact that PSR visits and free drug samples have on physician prescribing
behavior. In point of fact, much of the evidence on PSR effectiveness is anecdotal. The empirical
studies investigating the issue have been subject to data or methodological limitations that restricted
the ability to control for potential biases and have come to contradictory conclusions regarding even
the central issues: the effects of detailing on prescriptions (e.g., Parsons and Abeele 1981 vs. Gonul
at al. 2001), detailing on price elasticity (e.g., Rizzo 1999 vs. Gonul at al. 2001), and even price on
sales (e.g., Rizzo 1999 vs. Gonul at al. 2001).
Interestingly, even competing perspectives as to the role of PSRs, e.g., whether they are pro-
competitive or anti-completive in terms of influencing price elasticities (Rizzo 1999, Gonul et al.
2001), share a common view that PSRs have a substantive impact on physician prescribing behavior.
While possible, alternative considerations give rise to a third perspective suggesting that the impact
of PSRs on physicians may well be minimal. For example, other sources of information (colleagues,
3
scientific papers, and the physician’s own training and experiences) are also available to physicians
and these sources are likely to exert a much greater impact on prescribing choices. In addition,
counter to interpretations of empirical results associated with the two primary views, a non-causal
explanation may account for some of the observed correlation between physician prescribing
behavior and PSR activity. That is, both physician prescribing behavior and PSR activity are
influenced by some common factors such as physician practice size, i.e., bigger practices prescribe
more and will receive more visits and free samples. It is necessary to control for these non-causal
influences in order to properly assess the effect of PSR activity on physician behavior.
We have obtained access to a unique database that allows us to undertake econometric
analysis that overcomes a number of fundamental limitations existing in past research. In particular,
making use of a dynamic fixed-effects distributed lag model that accounts for physician-specific
effects likely to induce bias if left uncontrolled, we assess the effect of detailing and sampling on
physician prescribing behavior. The large number of observations in the database (it involves 3 drugs
and 24 monthly observations for 74,075 physicians, i.e., over 2 million observations in total) allows
us to accurately pinpoint the impact interactions with PSRs have on the number of new prescriptions
issued by physicians.
We find that while detailing and free drug samples have a positive and statistically significant
association with the number of new prescriptions issued by a physician, the magnitudes of the effects
range from modest to very small. As such, our results contradict the two dominant views and support
the contention that rather than being “easy marks,” physicians are “tough sells.”
Potential Limits to PSR Influence on Physicians
While most discussions of PSRs have focused on the factors facilitating their influence, less
attention has been directed at the factors limiting this effect. Unquestionably, PSRs provide
physicians with information about new and existing drugs. As PSRs are trained in persuading
physicians, detailing takes the form of presenting facts and, as has been documented (Zigler, Lew,
4
and Singer 1995), misrepresenting facts about the drug in an effective manner. Physicians can come
to rely on this information and change their prescribing practices accordingly. PSRs can induce trial
of new drugs to the extent that they may be the main channel of information dissemination about new
drugs and new indications for established drugs. The use of samples facilitates this process.
However, a number of conditions are present to suggest that despite their informative and persuasive
capabilities, PSR influence might be minimal.
Most importantly, PSRs are not the only or even the primary source of information about
drugs for physicians. Scientific papers, advice from colleagues, and a physician’s own training and
experience also influence prescribing practices. Indeed, most physicians view these other influences
as far more important than that of PSRs. Peay and Peay (1990) report that out of fifteen potential
information sources about drugs physicians rated PSRs twelfth in usefulness. It is not that PSR do
not provide information. Rather, the consideration is that other sources of information are relied on
much more frequently than PSRs.
PSR influence is limited by the fact that many physicians view skeptically or hold negative
attitudes toward PSRs (Lichstein, Turner, and O’Brien 1992, McKinley at al. 1990). Attribution
theory suggests that with low source credibility, which is determined by factors such as a source’s
trustworthiness and expertise (Dholakia and Sternthal 1977), arguments in a message will be
discounted (Eagley and Chaiken 1975). Physicians recognize that PSRs are neither experts, nor
necessarily trustworthy and realize that information presented is biased toward the promoted drug
and is unlikely to be objective, or even accurate (Connelly at al. 1990). Thus, physicians will
discount information received from a PSR. Since physicians have access to alternative sources of
information, which are more highly regarded, PSR influence may be very limited indeed.
Some additional characteristics of physicians would seem to make them particularly “tough
sells.” For example, the Friestad and Wright’s (1994) persuasion knowledge model suggests that
targets of persuasion use their knowledge about the persuasion agent and can effectively cope with
5
and even achieve their own goals during a persuasion attempt.1 Tests of the persuasion knowledge
model revealed that busy targets with accessible agent motivation are particularly effective in
resisting persuasion, e.g., they had the lowest evaluation of salesperson’s sincerity and the greatest
number of suspicious thoughts (Campbell and Kirmani 2000). Physicians fit the profile of such
targets: they do not allot much time to a PSR as they are busy and well aware that the PSR is trying
to persuade them to prescribe more of his company’s drugs.
When cast within the workings of other sources of influence, we would expect the ability of
PSRs to influence physician behavior to be relatively small. As such, we hypothesize a relatively
small effect of PSR activity on physician prescribing behavior.
Previous Empirical Research
The various studies assessing the effect of PSR activity on physician prescribing behavior
have generated conflicting results. Indeed, on some of the most central issues, ranging from the
effects of detailing on prescriptions, detailing on price elasticity, and even price on sales, studies
have come to diametrically opposite conclusions. Methodological limitations, however, call into
question inferences drawn from these analyses.
A few studies originating in the medical community are in the spirit of controlled randomized
experiments, which are the “gold standard” in medical research. These studies compare physicians
who did not see or were visited less by PSRs to physicians who were visited or visited more
frequently by PSRs (Chren and Landfeld 1994, Powers 1998). For example, Powers (1998)
compared the prescribing behavior of 31 family practitioners versus 47 physicians in general internal
medicine. The study finds that family practitioners prescribe more costly drugs than do internists. As
family practitioners are visited more frequently by PSRs than are those in general internal medicine,
the study attributes differences in behavior to PSR influence. The question unanswered is whether
1 Very often this goal is obtaining free drug samples (Medical Marketing and Media 2000) that they can later distribute to patients (Wolf 1998).
6
differences other than PSR activity (e.g., differences in type of patient seen) account for some of the
difference in behaviors. More broadly, the limitation of these studies is that, despite claims to the
contrary, they are not randomized in that PSRs do not determine which physicians to visit on a
random basis. Rather, PSRs are going to see physicians more likely to utilize the drug or who
prescribe in higher volume. This consideration invalidates these attempts to assess the effect of PSRs
independent of controls accounting for motivation influencing PSR behavior.
The ability to potentially control for other influences is an advantage of regression based
analysis. Past research has made use of different regression techniques to assess PSR influence.
Unfortunately, here too past research has been inadequate in controlling for physician-specific
effects.
Parsons and Abeele (1981), based on data for 24 months and 14 territories, model the number
of prescriptions sold in a given territory for a given month as a function of sales calls. The sales call
effect is allowed to vary depending on samples and handouts. Interestingly, while sales call elasticity
was positive when evaluated at the average number of samples and handouts, the estimated main
effect of detailing was negative. While Parsons and Abeele (1981) do not report the inflection points,
their model implies that at low and at high levels of handouts and samples, increases in detailing lead
to decreases in sales. The most dominant explanatory factor in their model is sales lagged one period,
which would reflect persistence in behaviors and carryover effects magnifying the influence of
detailing. Alternatively, lagged sales could be reflective of territory-specific effects that are not
modeled and, as such, could lead to biased estimates. Wotruba (1982), for example, raises this
possibility of territory specific effects (which might also be cast as a simultaneous equation bias issue
rising from an effect of prescriptions on detailing) to question the reported effects of detailing.
Rizzo (1999), based on annual data for the period 1988-1993 and 46 drugs, estimates a model
linking prescriptions for a drug for a given year to pharmaceutical company marketing activities
including price and detailing. He finds that price is negatively related to sales and that detailing is
7
anti-competitive in that it decreases price sensitivity. Detailing is also found to have a direct positive
effect on sales. We have concerns over the results as the model does not control for the persistence
of sales. Rather than modeling the growth rate in sales or including lagged sales as an explanatory
factor, as would be expected given the well known autocorrelation in sales, no consideration is given
to the dynamic properties of sales. The model has the classic spurious regression characteristics, i.e.,
very high R2 in the presence of substantial unmodeled autocorrelation. As such, little confidence can
be attached either to the point estimates or standard errors reported in the analysis.
A recent study commissioned by the Association of Medical Publications
(www.rappstudy.org) made use of monthly data over 5 years for 391 brands to investigate the impact
of pharmaceutical marketing practices. The study includes brand dummy variables to capture brand-
specific effects. Unfortunately, too little diagnostic information is reported, e.g., neither coefficient
estimates nor standard errors are supplied. A number of basic modeling issues are not addressed in
the analysis. For example, it is unclear whether simultaneity is present (e.g., are brand promotional
budgets a function of sales?) and what effect modeling feedback effects would have on the analysis.
Further, while a presumed exogenous trend variable is used to capture market dynamics,
autocorrelation widely acknowledged and shown empirically to be present in almost all sales series is
not taken into account. It is unclear how estimated effects, standard errors, or model implications
would have been impacted by modeling the persistence in sales, e.g., reported effects would not
reflect carryover effects inherent in an autocorrelated sales series. Given these unaddressed issues,
we can note problems in the analysis but cannot even speculate as to the direction of the bias.
Gonul et al. (2001), based on data involving 1785 patient visits, estimate a multinomial logit
model assessing factors influencing physician prescribing behavior. Exactly opposite to the findings
of Rizzo (1999), they report that price has a positive effect on prescription probabilities and that
detailing increases price sensitivity. They find statistically significant positive effects for detailing
and sampling, i.e., PSR activities increase the prescription probability of a drug, but do not discuss
8
the implications of the magnitude of the effects. These magnitudes can be calculated based on the
reported descriptive statistics and imply elasticities that are surprisingly large. The elasticity
estimates for the seven drugs studied, evaluated at the mean level of detailing and sampling, average
41% for detailing and 48% for sampling.2 As the effects of detailing and sampling dissipate only
inconsequentially in their model, a change in PSR activity will have not only current-term influence
but also similar longer-term effects on purchase probabilities. Particularly for samples that have a
negligible marginal cost (regardless of the retail price), their estimated coefficients imply enormous
returns to enhanced PSR activity. In point of fact, these substantial effects may be arising not from
the influence of PSR activity, but rather may be an outgrowth of a joint correlation with an omitted
factor from the model, e.g., larger practices prescribe more and receive more free samples.
A concern, which Gonul et al. (2002) explicitly acknowledge, is over the role of physician-
specific effects that may induce a bias in their estimated coefficients. They state (page 84):
“prescription behavior patterns might be strongly influenced by factors other than the explanatory
variables we include in our model. Examples are physicians’ unobservable personal
characteristics… Ignoring these factors might bias the coefficients of the included explanatory
variables.” The extent to which their estimates are biased by the failure to control for unobservable
factors remains unanswered, but this is one consideration that might account for the large estimated
effects.
Empirical Analysis
A key benefit of utilizing pooled time series cross-sectional (i.e., panel) data is the ability to
test for and control for the effect of unobserved fixed factors (Hausman and Taylor 1981). These
2 The elasticity of prescription probability Pj to covariate xjk in a conditional logit model is (∂Pj/ Pj)/ (∂xjk/ xjk) = βk*xjk*(1- Pj). Elasticity estimates are not constant across physicians as, for example, they would be higher for physicians one standard deviation above the mean in terms of detailing and sampling. As the authors’ model includes interactive effects involving patient characteristics, elasticity also varies across patients. They would be lower, for example, for patients on Medicare and in HMOs.
9
unobserved factors, if left uncontrolled, can induce bias in the coefficient estimates of the
explanatory factors included in the model. Past research, however, has either not used panel data or
not made full use of the benefits of panel data analysis. As such, caution needs to be exercised in
interpreting the findings from past research and suggests the need for additional study. We make use
of pooled time series cross-sectional observations (i.e., 24 months of observations across 74,075
physicians) and panel data statistical methods (i.e., a dynamic fixed effects distributed lag regression
model) to assess the effect of detailing and sampling on physician prescribing behavior.
Data
Access to all the data used in the study was gained from a US pharmaceutical manufacturer
with the only condition being that of insuring the anonymity of the firm and the drugs in the study.
Two different sets of data were merged to form the database. One data set pertains to the number of
new prescriptions, i.e., number of new scripts, issued by physicians during a month for a given drug.
As it is based on new scripts issued, our “new prescription” measure reflects both new and repeat
usage, but not refills accompanying the prescriptions. These data cover a 24-month period for 3
widely prescribed drugs. Thus, the total data sample we have available involves 74,075 US
physicians who fall into the top six deciles in terms of their prescription volume for these drugs at the
beginning of the data-reporting period.3 Also provided was the monthly number of new prescriptions
issued by each physician for competitor drugs in the corresponding therapeutic area.
The second data set pertains to detailing and sampling activity by PSRs for the same 3 drugs.
The company requires PSRs to provide information on the number of free drug samples left with a
physician, which is tracked by physician signature and ID number, and is recorded along with the
PSR’s report on each detailing visit. The two data sets were merged into one database containing
3 The company providing the data tracks only those physicians who show at least some prescribing activity or receive some detailing and sampling. Our analysis pertains to this group of physicians and we cannot make any assessment as to the potential responsiveness of those physicians who rarely, or never, prescribed one of the drugs we study or were not visited by PSR’s (e.g., the bottom 4 deciles).
10
information by month and physician on the number of new prescriptions issued for a drug, the
number of detailing calls physician received that month for the drug, the number of the free drug
samples the PSR left with a physician, and the number of new prescriptions physician issued for
competitor drugs.
To reduce the possible influence of extreme values (outliers), which would arise from, for
example, data entry errors and the common practice of one physician signing for all samples that
later get distributed to a group of physicians present at a continuing medical education (CME)
meeting or conference, we excluded the top 0.5% of observations for the number of details, samples,
and new prescriptions.4 While perhaps excluding some relevant information, the remaining data will
depict the typical relationship that arises between PSR activity and new prescriptions issued by
physicians for these drugs.
Table 1 presents basic background information and descriptive statistics for the drugs
included in our study. The drugs differ on a variety of dimensions: they have been on the market
from less than one year to 11 years; annual sales range from under $.5 billion to over $1 billion; they
come from different therapeutic areas. While the effect of detailing may vary across drugs, analysis
of these 3 drugs offers some generalizable insights not only because they provide a cross-section of
drugs in the marketplace but because they represent over 4 million PSR interactions with physicians.
Model
We employ the following dynamic fixed effects distributed lag regression model to assess the
effect of detailing and sampling on new prescriptions:
4 As we later report, we undertook sensitivity analysis on alternative definitions of outliers (e.g., 0%, .5%, 1%, 5%). The results are in close correspondence across these alternative data samples.
11
[1] Prescribeit= αi + βj*Detailsit-j + γj*Samplesit-j + ∑ λj*Competitorit-j +
φj *Prescribeit-j + ∑ δ
∑=
6
0j∑
=
6
0j
Τ
=1
=
6
0j
∑=
6
1j ττ *Time(τ) + κs*Specialty(s)*Trendt + εit ∑
=
11
1s
where Prescribeit, Detailsit, Samplesit, and Competitorit are, respectively, the number of new
prescriptions issued, the number of PSR visits, the number of free drug samples received, and the
number new prescriptions issued for competitive drugs by physician i at time period t. Time(τ) is an
indicator function that takes on the value 1 when the time period is τ, 0 otherwise (i.e., separate
dummy variables for each monthly time period), Specialty(s) is an indicator function that takes on
the value 1 when the specialty area of the physician is s, 0 otherwise (i.e., separate dummy variables
for each of the 11 specialty areas), and Trend is the observation number for a given month and year.
Since it includes both current-term and lagged variables in the model, Equation 1 allows for a wide
range of possible effects and influences, e.g., serial correlation (current-effects) and state-dependent
(persisting) dynamic relationship.
A key characteristic of Equation [1] is that it allows for a physician-specific effect, i.e., the
intercept αi is allowed to vary by physician. This consideration acknowledges that physician
behavior patterns are influenced by unobserved or unobservable factors, e.g., physician
characteristics. To the extent that these unobserved factors are correlated with detailing and
sampling, analysis not controlling for their effects will result in biased estimated effects for the
marketing phenomena. While we later use a Hausman (1978) specification test to empirically assess
the role played by fixed effects, we have a priori reason to believe that these unobserved factors will
in fact be correlated with marketing activity. For instance, larger practices will generate more
prescriptions and will also attract more detailing. As such, a spurious positive correlation, i.e.,
12
unrelated to any potential effects of detailing, will exist between detailing and prescriptions due to a
joint correlation with practice size.
As the effects of PSR activity are unlikely to be limited to the month when the visit occurred,
we allow for current and lagged effects for both detailing and sampling. The number of observations
available in our data sample allows us to directly estimate separate effects for lagged term rather than
imposing a specific decay pattern as a necessity for preserving degrees of freedom. We do, however,
need to specify the length of time that a PSR visit might influence physician behavior. We select a 6-
months lag length under the view that the effect of a visit will dissipate substantially by this period,
but do test for longer-term lagged effects as well. Still, we expect the effects of detailing to be
largest in the months closest to the visit. The cumulative direct effect of detailing and sampling can
be obtained simply by summing the coefficients, i.e., and γj. ∑=
6
0jjβ ∑
=
6
0j
Lagged values for new prescriptions (Prescribeit-j) capture autocorrelation in the series that
arises through inertia and persistence in physician behavior. These autoregressive effects play a key
role in that they magnify the effects of detailing and sampling. That is, the total effects of detailing
and sampling involve both a direct effect on prescriptions and an indirect effect that arises through
persistence in physician behavior. As such, the total effect of detailing and sampling can be
calculated as / [1- φj] and γj / [1- φj], respectively. ∑=
6
0jjβ ∑
=
6
1j∑
=
6
0j∑
=
6
1j
As we include both lagged own prescriptions and lagged competitors’ prescriptions, the
model separates lagged total demand dynamics into two key components: competitive substitution
and own demand growth. Lagged competitors’ prescriptions will have a negative impact on
prescriptions as they capture the substitution effects that physicians make between competing drugs.
The current competitive prescriptions, however, will capture two different phenomena: they will
reflect not only substitution effects but also changes in total demand due to market expansion or
13
contraction. In this regard, current-term competitive effects will be acting as a proxy for two
different phenomena with opposite effects, i.e., negative substitution effects and positive market
demand effects. As such, the current-term coefficient (λ0) will depend on the relative magnitude of
the two conflicting effects and, therefore, the sign of the effect cannot be postulated a priori.
The other variables in Equation [1] are time-period-specific intercepts and specialty-specific
trends. The time-period-specific intercepts (the coefficients δτ) allow for the fact that the number of
prescriptions may differ across time periods. These intercepts capture not only seasonal effects but
all brand-wide influences that shift prescribing behavior across all physicians (e.g., price changes,
changes in the set of alternative medications available, changes in advertising campaigns, etc.). That
is, the inclusion of the time specific dummy variables will capture all effects common across
physicians, which would include the diffusion pattern for the drug, research reports in scientific
journals, any negative or positive publicity for the brand or its competitors, etc. The 11 specialty-
specific trends κs capture influences that shift prescribing behavior across all physicians in a
particular specialty.
In order to remove the influence of physician specific effects (i.e., αi), we take first
differences of Equation 1 to obtain:5
[2] ∆Prescribeit= βj*∆Detailsit-j + γj*∆Samplesit-j + λj*∆Competitorit-j +
φj*∆Prescribeit-j + ∑ δ
∑=
6
0j
∑=
6
1
∑=
6
0j
Τ
=1τ
∑=
6
0j
∑=
11
1sjτ
*∆Time(τ) + κs*Specialty(s) + ηit
5 Taking mean differences (which is equivalent to having a dummy variable for each physician) is an equally efficient alternative to taking first differences of the data to remove the fixed effect. The first difference estimator offers considerable advantages to the mean difference estimator, however, in the presence of dynamic effects or simultaneity. For example, while an instrumental variable approach generates consistent estimate of the first-order autocorrelation coefficient for the first difference estimator, the mean differences estimator will be inconsistent. In the presence of simultaneity, lagged values can be used for instruments for the first difference model but they are not valid instruments for the mean difference estimator.
14
As we do not have data on the marketing activities of competitors, we cannot assess
competitive marketing effects. The model, however, does have a mechanism to control for their
influence. Competitor sales will to a large extent capture these effects and reduce potential omitted
variable bias. That is, to the extent that changes in firm and competitor marketing activities are
correlated across physicians (low correlation between changes in firm’s and competitors’ marketing
activities would limit the extent of this bias), not accounting for competitive marketing activity
would result in biased estimates of the own detailing and sampling effects. However, since
competitor marketing will influence competitor sales, the competitor sales variable in our model will
act as a proxy variable (Wickens 1972) for competitor marketing expenditures and, as such, reduce
potential omitted variable bias.
We estimate Equation [2] using instrumental variable estimation as ordinary least squares
will generate biased estimates of the coefficients for ∆Prescribeit-1 and ∆Competitorit. By
construction ∆Prescribeit-1 will be correlated with the differenced error term ηit and just as
substitution effects cause competitor prescriptions to influence own prescriptions, own prescriptions
will influence the amount of competitor prescriptions. We use lagged values of the series, i.e.,
Prescribeit-2, Prescribeit-3, Prescribeit-4, Prescribeit-5, Prescribeit-6, and Competitorit-2,
Competitorit-3, Competitorit-4, Competitorit-5, Competitorit-6, to generate instrumental variable
estimates for ∆Prescribeit-1 and ∆Competitorit. This procedure generates consistent (i.e.,
asymptotically unbiased) estimates of the parameters and their standard errors (Anderson and Hsiao
1982).6
6 As our dependent variable is the number of new prescriptions issued, initial inclinations might suggest the applicability of count data regression methods, e.g., the Poisson or negative binomial estimators. A number of considerations, however, point to the advantages of the fixed effect estimator we employ. The applicability of our estimator stems from the fact the error term in Equation 2 is “reasonably well” approximated by a normal distribution. Consistent with a normal distribution, the skewness of the error term is near zero. The fact that we take differences of the data transforms the data from a non-symmetric to a symmetric distribution. The kurtoses for
15
Results
For each of the 3 drugs in our study, we estimated the Equation [2] regression model. Table
2 reports the estimated coefficients. Figures 1 and 2 graphically depict the estimated effects of
detailing and sampling, respectively.
Persistence in Prescribing Behavior
For each of the three drugs in the study we observe significant persistence in physicians’
prescribing behavior. While the first order autocorrelation is the most substantial for all three drugs,
significant higher order effects are present as well. For Drug A the estimated coefficients for month 1
through 6 of .357, .205, .111, .04, .004, and .017 imply a total persistence of .734 (std.=.049). For
Drug B we observe lower levels of persistence with the estimates decreasing from .208 in month 1, to
.143, to .099, to .06, to .012, and to .007 in month 6. Total persistence for Drug B is .529 (std.=.022).
Drug C prescriptions exhibit even lower persistence with estimates of .078, .033, .026, .012, -.006,
and .012 for month 0 through 6. The total persistence for Drug C is only .156 (std.=.031).
Detailing
For each of the three drugs in the study we observe statistically significant positive, albeit
rather small, effects of detailing on prescriptions. Both current-term and carryover effects exist. For
Drug A, statistically significant positive effects are present contemporaneously and for the
subsequent 4 months, (.120, .103, .062, .065, .047, respectively). The effects for months 5 and 6,
i.e., .003 and .016, are statistically insignificant. The cumulative direct effect that an additional PSR
the error terms for the 3 drugs in our study are 3.9, 3.4, and 2.4, respectively, as opposed to 3.0 for the normal distribution. The differences, however, will not impact the coefficient estimates (least squares is still efficient in the class of linear estimators) and will have a barely discernable impact on confidence intervals. While a fixed effect Poisson regression would be an inappropriate estimator as our data are over-dispersed (the Poisson model in based on the assumption that the variance of the data is equal to the mean), a fixed effect negative binomial estimator has merits. However, existing methods and statistical properties for this type of estimator are not well-developed for the type of model we propose. In particular, existing estimation methods (i.e., Hausman, Hall and Griliches 1984) have been questioned as to their ability to in fact control for time-invariant covariates (Allison and Waterman 2002), have not yet been developed or had their statistical properties assessed for dynamic models allowing for persistence (Greene 2001), and prohibit the use of lagged variables for instrumental variable estimation. If and when these issues become resolved, we would expect little (if any) difference between the results obtained from the estimation procedure we employ and those obtained from a fixed effects negative binomial estimator.
16
visit has on the number of new prescriptions (i.e., the sum of the estimated coefficients) is .415
(std=.089). The total effect that detailing has on prescriptions depends jointly on this direct effect
and on the indirect effect that arises through the persistence of physician behavior. Accounting for
both these effects (calculated as ∑ / [1- φj]) yields an estimated total effect 1.56, with a 95%
confidence interval of [.80; 2.23].
=
6
0jjβ ∑
=
6
1j
7 That is, on average, a PSR visit generates approximately one and
one-half new prescriptions of Drug A.
The estimated response to a change in PSR visits for Drug B is similar to Drug A in that we
observe a statistically significant response the month of the visit that diminishes over the subsequent
6 months. The magnitude of the effect, however, is smaller. The estimated effects for months 0
through 6 are .054, .033, .026, .023, .014, .002 and -.001. These sum to a cumulative direct effect of
.151 (std=.029). Once we consider the persistence in the prescribing process, the total effect of one
detailing visit for Drug B is estimated at .32, with a 95% confidence interval of [.219; .428]. In other
words, on average, it takes an additional 3.11 PSR visits to generate an additional new prescription
for Drug B.
For Drug C we again observe similar results in that the estimated effect of a PSR visit is
statistically significant, but small in magnitude. The estimated effects for months 0 through 6 are
.021, .028, .024, .021, .012, .011, and .010, respectively. All estimates are statistically different from
zero. The estimated cumulative direct effect of .129 (std=.024) is the smallest of the three drugs
studied. Further, as Drug C prescriptions exhibit the lowest persistence, the total effect of one
detailing visit for Drug C is also the smallest at .153, with a 95% confidence interval of [.105; .201].
7 As the estimated total effect involves the ratio of normal variables, its distribution will be non-normal. We make use of simulation methods based on the Model [2] coefficient estimates, their variance-covariance matrix, and 10,000 draws to construct confidence intervals (Krinsky and Robb 1986).
17
This indicates that it would take an additional 6.54 PSR visits to induce one additional new
prescription of Drug C.
Sampling
We also observe statistically significant but small effects for sampling. Sampling for Drug A
has a positive and statistically significant contemporaneous effect (.018), but statistically
insignificant effects for months 1 through 6 (.002, .006, .006, .004, .007, and -.003, respectively).
The estimated cumulative direct effect across the six months is .041 (std=.02). The total (direct and
indirect) effect of one free sample of Drug A is .155, with a 95% confidence interval of [.032; .310].
As such, on average, an additional 6.44 samples are needed to induce one additional new prescription
of Drug A.
We see a smaller response for sampling for Drug B than for Drug A. A change in sampling
has statistically significant positive, albeit declining, effects for each month (.006, .003, .002, .002,
.002, .002, and .001 for months 0 through 6, respectively). The estimated cumulative direct effect
across the six months is .019 (std.=.004). The total effect of one free sample of Drug B is .039, with a
95% confidence interval of [.025; .054]. It would take 25.39 additional samples to generate one
additional new prescription for Drug B.
The estimated response to sampling is smallest for Drug C. The estimated effects are .007,
.003, .001, .0005, -.0003, .00001, and .0001, with only the contemporaneous and 1 month lag effects
being statistically significant. The estimated cumulative direct effect is .012 (std.=.005). Since the
persistence level is very low for Drug C, the total effect of one free drug sample is only slightly
higher at .014, with a 95% confidence interval of [.0042; .0232]. This means that it takes 73.04
additional samples of Drug C to generate one new prescription.
Competitive Prescriptions
As discussed earlier, the instrumental variable for the contemporaneous competitive
prescriptions captures 2 distinct phenomena with two distinct effects, i.e., a positive effect of growth
18
in total demand and a negative effect of brand switching. The positive contemporaneous effect
observed for Drugs A and B is consistent with the growth in demand effects dominating brand
switching. For Drug C, the statistically insignificant estimate implies that contemporaneously the
market growth effects essentially cancel out the brand switching effects. As expected, consistent with
brand switching, we observe negative effects for lagged competitive prescriptions. The inclusion of
these competitive effects in the model is important not only in helping explain new prescriptions but
also in allowing us to isolate the persistence in physician behaviors. That is, since competitive
prescriptions are correlated with own prescriptions, failure to model these competitive effects would
results in biased estimates of the autocorrelation coefficients and, as a result, biased estimates of total
detailing and sampling effects.
Other Influences
The model also includes dummy variables capturing time-period specific effects (as our
model involves first differences of the data and 6 lags, time period 1 is the 8th month of data in our
24 months sample) and differences among specialties. While we find some specialty area effects and
time-period specific differences, little correlation exists, however, between the change in detailing or
sampling and these control variables. As such, their inclusion in the model has little impact on the
estimated direct effects of detailing or sampling. It does, however, significantly affect the estimates
of persistence. Failure to control for unobserved time-period specific influences on prescribing
behavior leads to biases in the estimates of persistence and, therefore, biased estimates of total
detailing and sampling effects. In Appendix A we provide additional discussion of this issue.
Model Validation and Sensitivity Analysis
We undertook a number of sensitivity tests to assess the validity of the model [1] and stability
of our results. In all cases, we found no evidence that calls into question the results we report. For
example, we modified Equation [2] to allow for the possibility of longer lagged effects of detailing
and sampling. The estimated effects for months 7 through 12 were small and statistically
19
insignificant. The results were not sensitive to the inclusion or exclusion of outliers. Estimating
model [2] with a data set that either excludes more extreme values or includes more extreme values
produced results in close correspondence to those reported. We also allowed for the possibility of
feedback effects (i.e., simultaneity) as the change in new prescriptions may influence the change in
detailing and sampling. A Hausman (1978) specification test failed to reject the null hypothesis of no
such feedback. We tested alternative functional specifications but found no evidence of non-linearity
in the relationships.8 For example, we failed to observe a non-linear detailing response function
(e.g., squared-terms were insignificant and a piece-wise regression model failed to show any
difference in estimated coefficients for physicians with above versus below average detailing
activity). We also failed to observe non-linearities associated with interactive effects (e.g.,
interaction terms involving detailing and sampling were insignificant).
While consistent, the estimates we report would not be efficient if in fact physician-specific
effects were not present. Equation 1 with a uniform constant (α), rather than a constant varying by
physician (αi), would generate more efficient estimates under this scenario. A Hausman (1978)
specification test, however, rejects at above the 1% level the hypothesis of a uniform constant.9 Not
modeling the physician-specific effects results in biased estimates of not only the coefficients for
PSR activities but also the estimates of the autocorrelations in new prescriptions. The biases are
particularly severe for the estimated effects of sampling. The estimated total effects of sampling
from the model ignoring fixed effects are on average 5 times greater than those we report. The
8 It is interesting to note, however, that model specifications ignoring the presence of fixed effects display the presence of significant non-linearity. The failure to control for these fixed effects might help in explaining some non-linearities reported in previous research. 9 Under the hypothesis of the fixed effects being uncorrelated with the explanatory factors in the model, both the random effects model (i.e., a model with a uniform constant) and the fixed effects estimators yield consistent coefficient estimates. The random effects estimator will be efficient, but the fixed effects estimator will not. As such, under the null hypothesis, estimates from the two models should not differ systematically. Under the alternative hypothesis of the fixed effects being correlated with the explanatory factors, the fixed effects estimator will be consistent but the random effects estimator will not. The Hausman specification test assesses the difference in the coefficient estimates between the models and, therefore, provides a test of the different model assumptions.
20
Hausman specification test documents the presence of significant physician-specific fixed effects and
strongly rejects the “naïve” (i.e., no-fixed-effects) model specification. A failure to control for these
effects in the “naïve” model generates biased estimates of PSR influence.
In addition to the modeling of physician-specific effects, the modeling of persistence in
physician behavior also plays a key role in influencing estimates of the detailing and sampling
effects. That is, as physician persistence magnifies influences, substantial differences can exist
between estimates of direct effects and total effects. As mentioned previously, we find that the
estimates of persistence (i.e., the coefficients for lagged prescriptions) depend on the inclusion of
lagged competitor prescriptions in the model. Estimates of persistence are substantially lower across
all the drugs in the study (in two cases close to zero) if higher-order lags of own and competitor
prescriptions are not included in the model as well. This finding follows directly from the standard
omitted variable bias consideration, i.e., leaving out a variable, which is negatively correlated with
the dependent variable but positively correlated with an included variable, results in a downward bias
in the estimates of the included variable. This consideration is one factor that might explain why we
find persistence in physician prescribing behavior while some other studies that allow for a dynamic
effects framework but lack the competitive prescribing data are unable to detect it (e.g., Manchandra
et al. 2000, 2003). In Appendix A we provide further discussion of some alternative models and how
differing types of model mis-specification influence the estimated effects of detailing and sampling.
We have also investigated the possibility that data reporting problems (i.e., measurement
error) might be biasing our estimates of the effect of detailing downward. Both random
measurement and systematic error (PSRs might be motivated to over-report either the number of
drugs they promoted to a physician on a particular visit or the number of visits that occurred) might
lead to a bias towards zero in the estimated effect of detailing. To assess this possibility we estimated
our model including only those details that were also accompanied by drug samples. We can be
reasonably certain that these details did in fact occur, as the sampling data is recorded by a third party
21
from the receipt slips signed by the physician receiving the free samples. The estimates of the
detailing effect obtained from estimating Equation [2] on this restricted data sample are
indistinguishable from those we reported in Table 2. As such, we have no reason to believe that our
results are driven by measurement error bias.
The possibility still exists that some characteristics of the drugs in our study may differ from
those where detailing is effective. That is, our results may capture the effect of detailing and
sampling for the drugs studied, but these drugs may not be reflective of drugs where PSR activity is
likely to be influential. For example, PSR activity might be posited to be more effective for new as
opposed to established drugs. This could account for the modest effects found for drugs A and B.
Drug C was new to the market. It had, however, disappointing sales. Might the effects of PSR’s be
greater for drugs, new to the market, that ultimately achieve success in the marketplace? To answer
this question we obtained data on a fourth drug, which was new to the market and achieved
commercial success during the period of study. It also differed from the drugs in our study in that it
was in a new therapeutic class and had few (only one) direct competitors. Despite these differences,
estimation of Equation [2] for this fourth drug generated similar results to those obtained for the
other drugs on our study. The estimated cumulative direct effects were .15 for detailing and .013 for
sampling. With an estimated persistence of .25, this gave rise to total effects for detailing and
sampling of .20 and .017, respectively. As such, we find no evidence to questions the generality of
our findings based on unique features of the three drugs in our study. Analysis of this fourth drug
generates findings very similar to those that we observe for Drug C.
While our sensitivity analysis failed to challenge the Table 2 results, additional investigation
is still warranted. A number of directions are of potential promise for future research. One direction
would involve assessing the characteristics of drugs that induce variation in PSR responsiveness.
That is, what can explain the differences in PSR responsiveness that we observe among the drugs
studied? A variety of factors, ranging from time on the market to the efficacy of the drug, might
22
induce differences in responsiveness. Further, analysis assessing which physicians are most
responsive to PSR influence and why this occurs would be of considerable value both from a public
policy standpoint and from the standpoint of increasing marketing’s understanding of factors
influencing responsiveness to sales force efforts. While our results provide aggregate effects,
differences in responsiveness may exist across physicians. Physician characteristics as varied as, for
example, specialty area, size of practice, gender, and age might be able to account for inter-physician
differences in responsiveness.
Discussion
The focus of our study was to assess the magnitude of physician responsiveness to two main
practices of pharmaceutical marketing while controlling for other possible influences on prescribing.
Are physicians ‘easy marks’? To the contrary, our results show that physicians are ‘tough sells’ in
that sales force activity has effects on prescribing behavior that range from modest to very small. For
the 3 drugs in our study the estimated total effects on new prescriptions are 1.56, .32, and .153 for
detailing and .155, .039, and .014 for sampling. In other words, physicians are most responsive to
PSR activities for Drug A where an additional prescription would arise from a .64 increase in
detailing or a 6.44 increase in sampling. They are least responsive to PSR activities for Drug C
where an additional prescription would result from 6.54 additional PSR visits or 73.04 additional
samples.
The high statistical significance of the estimates indicates that these marketing activities have
an effect on the number of new prescriptions. But, the magnitude of the effect indicates that PSR
activities have only a small impact. The large sample size provides small standard errors (allowing
us to distinguish between a very small effect versus a statistically insignificant effect) so that we are
able to accurately pinpoint just how small the positive effect is. The estimated effects are in some
cases an order of magnitude smaller than has been speculated based on anecdotal evidence or
reported in prior research.
23
Given the small response to PSR activity, the question is no longer “are physicians ‘easy
marks’?” but rather “why do drug companies make such extensive use of PSRs given their limited
effectiveness?” It appears that drug company profits might be enhanced (or drug prices reduced)
through costs savings achieved through a reduction in PSR numbers. While this may be so, some
additional issues need to be considered. First, it should be remembered that our estimates reflect the
effect of a visit on the sales of a single drug. As a PSR will discuss more than one drug during a
visit, the impact of a given visit will be greater than the effect on a single drug. Second, the reported
estimates relate to “new scripts” issued. Sales of the drug, however, will also be based on the refills
accompanying the prescription, which average between 2 and 3 for the drugs in our study. Both these
considerations magnify the financial implications of a detailing visit. Further, the margin to the
pharmaceutical firm on a drug can be considerable.10 These considerations lead us to believe that
the returns to detailing for Drug A are positive, which stems both from its larger margin and the
larger estimated physician response to detailing, but are negative for Drugs B and C.
Why would the firm engage in a practice that has negative returns? One possible explanation
is suggested by practitioners’ comments: “No one is really sure if sending the legions of reps to
doctors’ offices really works. Everyone is afraid to stop it, because they don’t know what difference
it’s making” (Narayanan et al. 2003). Indeed, the number of PSRs is now over 80,000; it has almost
doubled in the past five years, while the number of physicians remained constant (The Wall Street
Journal, April 23, 2002). For some drugs (e.g., those with lower margins) the current detailing system
may be sub-optimal, which might be a result of the intensive PSR ‘arms race’ of the 90s. This is
consistent with a recent McKinsey report (Elling at al. 2002) that questions the effectiveness of the
current PSR system and advocates that pharmaceutical companies transform their sales model.
10 An additional indirect effect may arise through word-of-mouth influence. That is, a detailing visit can influence the physician to use a drug who, in turn, influences other physicians. Indeed, PSRs desire to influence these opinion leaders because of this enhanced effect (McKinley at al. 1990, Goldfinger 1987). But, given the minimal direct effect of PSR influence, this indirect effect is unlikely to be substantial. Further, detailing may have an indirect effect on prescribing by influencing the process of drug addition to formularies.
24
We do not wish to make any value judgments about the magnitude of physician’s
responsiveness to PSR visits and the reasons behind it. Responsiveness may mean that physicians are
better internalizing information about a drug and the result is better patient outcomes or care at a
lower cost. Alternatively, responsiveness may simply reflect brand switching among drugs that
provide similar benefits. While drug company revenues would be affected, patient care or costs
would not. However, responsiveness to PSRs could end up in inferior patient care or in higher costs
when physicians prescribe, for example, branded drugs that are no more effective than a generic
equivalent but are higher priced (Gold 2001). Whatever the relative costs and benefits, the bottom
line remains that the average effect of PSR activity on physician prescribing behavior is small. The
public policy debate would be better served by recognizing the modest effect PSR activity has on
physician prescribing behavior.
25
Table 1 Drug Profiles*
Drug A
Drug B
Drug C Sales range ($US)** .5 to 1 billion over 1 billion under .5 billion Time on the market at the beginning of the recorded period.
3 years
11 years
6 months
Product Portfolio Position Rising Star Cash Cow Question Mark Estimated number of competitors in the respective therapeutic area
12
18
11
Mean number of details per physician per month
1.73 (1.75)
1.98 (1.70)
1.73 (1.44)
Mean number of free drug samples per physician per month
4.34 (9.76)
7.79 (13.71)
4.02 (7.73)
Mean number of monthly new prescriptions per physician
13.18 (14.81)
8.82 (10.43)
2.27 (3.58)
Average number of refills following one new prescription
3 3 3
Recommended duration of therapy‡
3 months, and as
maintenance with periodic patient reexamination
3 months and
up to 9 month
Not yet established
Cost relative to other drugs in the therapeutic area
Average Above average Average
Mean number of monthly new prescriptions per physician in the respective therapeutic area
42.91 (43.63)
48.80 (53.73)
22.46 (19.03)
Therapeutic Area is Relatively New Well Established Well Established Specialty area of Top Prescribers
Psychology and Psychiatry
Primary Care‡‡
Primary Care‡‡
Number of Physicians 10,516 55,896 30,005 Number of data points 252,384 1,341,504 720,120
________________________________ * Standard errors are in parentheses. The sum of the number of physicians in each of the three data sets is greater than the total number of physicians in the study (74,075) as some physicians are in the upper 60 prescribing percentile for more than one of the drugs in our study. ** We provide ranges for sales volume of each drug, as opposed to a specific number, to help insure the anonymity of the drug. ‡ as reported in Mosby’s GenRx reference for the relevant time period. ‡‡ The primary care specialty area includes family practice, general practice, internal medicine, and osteopathy.
26
Table 2 The Effects of PSR Detailing and Drug Samples on Physician New Prescription Issuing:
Equation [2] Estimates‡
Dependent Variable: ∆Prescribeit
Drug A Drug B Drug C
∆detailsit .120 (.015)* .054 (.005)* .021 (.004) * ∆detailsit-1 .103 (.019)* .033 (.006)* .028 (.005) * ∆detailsit-2 .062 (.020)* .026 (.006)* .024 (.005) * ∆detailsit-3 .065 (.020)* .023 (.007)* .021 (.006) * ∆detailsit-4 .047 (.020)* .014 (.006)* .012 (.005) * ∆detailsit-5 .003 (.019) .002 (.006) .011 (.005) * ∆detailsit-6 .016 (.015) -.001 (.005) .010 (.004) * ∆samplesit .018 (.003)* .006 (.0006)* .007 (.0007)* ∆samplesit-1 .002 (.004) .003 (.0008)* .003 (.0009)* ∆samplesit-2 .006 (.004) .002 (.0009)* .001 (.001) ∆samplesit-3 .006 (.004) .002 (.0009)* .0005 (.001) ∆samplesit-4 .004 (.004) .002 (.0009)* -.0003 (.001) ∆samplesit-5 .007 (.004) .002 (.0008)* .00001 (.001) ∆samplesit-6 -.003 (.003) .001 (.0006)* .0001 (.0008) ∆prescribeit-1
‡‡ .357 (.022)* .208 (.008)* .078 (.010)* ∆prescribeit-2 .205 (.013)* .143 (.006)* .033 (.008)* ∆prescribeit-3 .111 (.008)* .099 (.004)* .026 (.006)* ∆prescribeit-4 .040 (.006)* .060 (.003)* .012 (.005)* ∆prescribeit-5 .004 (.004) .012 (.002)* -.006 (.003) ∆prescribeit-6 .017 (.003)* .007 (.001)* .012 (.002)* ∆competitorit
‡‡ .25 (.050)* .738 (.050)* .030 (.040) ∆competitorit-1 -.041 (.0017)* -.022 (.0005)* -.004 (.0006)* ∆competitorit-2 -.038 (.002)* -.014 (.0007)* -.004 (.001)* ∆competitorit-3 -.032 (.002)* -.014 (.0006)* -.002 (.001) ∆competitorit-4 -.012 (.003)* .0014 (.0011) -.002 (.001) ∆competitorit-5 -.002 (.002) .005 (.0009)* -.001 (.001) ∆competitorit-6 -.006 (.002)* -.001 (.0005)* -.0005 (.0006) F-statistic
F (52, 149,413) = 45.03*
F(52, 851,244) = 169.34*
F (52, 455, 873) = 35.44*
_______________________________ ‡ Standard errors in parentheses. The model also includes time-period-specific and specialty-specific intercepts. The number of observations differs from that in Table 1 due to the taking of first differences, the inclusion of six lagged terms, and removing outliers. ‡‡Instrumental variable estimate utilized. * P value < 0.05
27
Figure 1 Direct Effects of Detailing on the Prescribing Behavior of Physicians*
Drug A
0.016
0.120.103
0.062 0.0650.047
0.003
-0.05
0
0.05
0.1
0.15
0.2
t t-1 t-2 t-3 t-4 t-5 t-6
Cha
nge
in th
e nu
mbe
r of n
ew
pres
crip
tions
Drug B
-0.001
0.054
0.0330.026 0.023
0.0020.014
-0.02
0
0.02
0.04
0.06
0.08
t t-1 t-2 t-3 t-4 t-5 t-6
Cha
nge
in th
e nu
mbe
r of n
ew
pres
crip
tions
Drug C
0.010.0110.012
0.0210.0240.028
0.021
-0.01
0
0.01
0.02
0.03
0.04
0.05
t t-1 t-2 t-3 t-4 t-5 t-6
Cha
nge
in th
e nu
mbe
r of n
ew
pres
crip
tions
_______________________________________ *Coefficient estimates from Equation 2. Numbers represent the additional number of new prescriptions a physician will issue in a given month following a one PSR visit increase in promotional effort occurring in the current month. Error bars represent 95% confidence intervals.
28
Figure 2 Direct Effects of Sampling on the Prescribing Behavior of Physicians*
Drug A
-0.003
0.0070.0040.0060.006
0.002
0.018
-0.02
-0.01
0
0.01
0.02
0.03
t t-1 t-2 t-3 t-4 t-5 t-6
Cha
nge
in th
e nu
mbe
r of
new
pres
crip
tions
Drug B
0.0010.0020.0020.0020.002
0.003
0.006
-0.002
0
0.002
0.004
0.006
0.008
t t-1 t-2 t-3 t-4 t-5 t-6
Cha
nge
in th
e nu
mbe
r of
new
pres
crip
tions
Drug C
0.00010.00001
-0.0003
0.00050.001
0.003
0.007
-0.004
-0.002
0
0.002
0.004
0.006
0.008
0.01
t t-1 t-2 t-3 t-4 t-5 t-6
Cha
nge
in th
e nu
mbe
r of
new
pres
crip
tions
_______________________________________ *Coefficient estimates from Equation 2. Numbers represent the additional number of new prescriptions a physician will issue in a given month following a one free drug sample increase in promotional effort occurring in the current month. Error bars represent 95% confidence intervals.
29
Appendix A
To better illustrate how various elements of Equation [2] influence the results we report in
Table 2, in Table X we present estimates from some alternative models for Drug B. As these models
are nested within Equation 2, the results show how different types of model mis-specification (i.e.,
omitted variable bias) influence the estimated effects of detailing and sampling. We have performed
similar analysis for the other two drugs and found results (i.e., direction and the relative magnitude of
the biases) very close to those we report here for Drug B. Panel A of the Table X presents four
different models that ignore the presence of time-invariant physician-specific fixed effect (αi). Panel
B of the Table X presents four models that account for fixed effects but ignore some other factors.
If Fixed Effects are Ignored (Table X: Panel A):
Model X.1 is the most basic specification that contemporaneously links the number of new
prescriptions to the level of detailing and sampling. The estimated effects of detailing and sampling
are significantly biased upwards. The relative magnitude of the bias is greater for the estimates of
sampling effects. Model X.2 is a Koyck model allowing for carryover effects. Similar to Model X.1
it reports biased upward estimates of the contemporaneous detailing and sampling effects. The
implied total effects are also biased upwards.
Model X.3 explicitly allows detailing and sampling activity to have not only
contemporaneous but also carry-over effects as well and, in contrast to Model X.2, does not impose a
specific decay structure on the carry-over effects. An interesting artifact of the Model X.3
(mis)specification is that the estimation results suggest little or no dissipation of detailing and
sampling effects. We report a 12-lag model in Table 3 Panel A for illustration. Even one year after a
detailing visit occurred or a free sample was issued, their effects are only slightly diminished. Model
X.3 demonstrates that ignoring a fixed effect and estimating a distributed lag structure (or using some
30
form of discounted cumulative detailing and sampling) may lead to erroneous conclusions about the
duration and the magnitude of the effects.
Model X.4 allows for persistence (autocorrelation) in prescribing practices. The estimated
effects of persistence for drug B are highly overstated. The implied total persistence is at .89. The
autoregressive coefficients are picking up the impact of the omitted fixed effect. Interestingly, many
lagged terms for detailing and sampling are negative and significant. Moreover, the implied
cumulative direct effect (and thus the total effect) of detailing in Model X.4 is negative and
significant.
A Hausman specification test documents the presence of significant physician-specific effects
in prescribing behavior. As such, the models in Panel A of Table X show how ignoring fixed effects
can lead to biased estimates that either overstate or understate the physician responsiveness to
marketing activity. The direction of the bias depends on the specifics of the estimation model. In the
next section we consider a set of models controlling for fixed effects but ignoring some of the other
elements in Equation 2.
When Fixed Effects are Modeled, but some Other Factors are Ignored (Table 3: Panel B):
Model X.5 is the most basic fixed effects specification that allows for physician-specific
effects and contemporaneous effects for detailing and sampling. By ignoring persistence and carry-
over effects, the estimated effects from this model understate both the direct and total effects for
detailing and sampling.
Model X.6 adds a distributed lag structure to assess possible carry-over effects of detailing
and sampling. In contrast to Model X.3, we observe carry-over effects with a clear dissipation
pattern. In six months the effects of detailing and sampling are fully dissipated. In contrast to Model
X.5, Model X.6 shows a significant increase in the direct effects of detailing and sampling. The
results differ from the Equation 2 estimates in that the total effect of detailing and sampling are
under-reported by not accounting for persistence.
31
Model X.7 addresses persistence in physician behavior by including a lagged dependent
variable.11 Compared to Table 2 results, the estimate of persistence in the specification is extremely
low: it suggests no persistence in physicians’ prescribing behavior. In fact, this result is a
consequence of omitted variable bias – a complex dynamic process determines persistence and we
need to model the dynamics of own and competitive prescriptions issuing to capture this process.
Finally, we want to comment on the role of the time-period specific intercepts in the
estimation model. These time-varying intercepts capture all the unobserved influences that drive
prescriptions across all the physicians in a given month (e.g., diffusion, rate of the drug addition
to the formularies, published scientific studies, new indications, etc.), but are not explicitly in the
model. All the alternative models we discussed so far included these time-period specific
intercepts. The last model we present, Model X.8, does not include time-period specific
intercepts. While the estimates of direct detailing and sampling effects remain unchanged, the
estimated total persistence is substantially biased downward by this omission. Since both direct
effects and persistence determine the total effects of marketing effort, leaving the time-period
specific intercepts out of the model may lead to erroneous inferences about marketing
effectiveness.
11 We use an instrumental variable estimation and do not discuss here the host of econometric problems that would result if instruments were not used.
32
Table X (Panel A) Alternative Model Specifications: Level Models Ignoring Physician-Specific Fixed Effects‡
Model X.1 Model X.2 Model X.3 Model X.4 detailsit .628(.004)* .164 (.003)* .084(.008)* .053(.005) * detailsit-1 .041(.008)* .012(.005) * detailsit-2 .036(.008)* .005(.005) detailsit-3 .033(.009)* -.004(.005) detailsit-4 .022(.009)* -.008(.005) detailsit-5 .009(.009) -.013(.005)* detailsit-6 .011(.009) -.014(.005)* detailsit-7 .032(.009)* -.001(.005) detailsit-8 .028(.009)* -.011(.005)* detailsit-9 .023(.009)* -.018(.005)* detailsit-10 .056(.009)* -.004(.005) detailsit-11 .060(.009)* -.016(.005)* detailsit-12 .080(.008)* -.022(.005)* samplesit .114(.001)* .030 (.0004)* .031(.001)* .012(.001)* samplesit-1 .026(.001)* .005(.001)* samplesit-2 .021(.001)* .002(.001)* samplesit-3 .020(.001)* .001(.001)* samplesit-4 .018(.001)* .000(.001) samplesit-5 .016(.001)* .000(.001) samplesit-6 .016(.001)* .000(.001) samplesit-7 .014(.001)* -.002(.001)* samplesit-8 .016(.001)* -.001(.001) samplesit-9 .015(.001)* -.001(.001) samplesit-10 .016(.001)* -.003(.001)* samplesit-11 .018(.001)* -.002(.001)* samplesit-12 .021(.001)* .002(.001)* prescribeit-1 .739 (.0006)* .273(.001)* prescribeit-2 .183(.001)* prescribeit-3 .133(.001)* prescribeit-4 .084(.001)* prescribeit-5 .048(.001)* prescribeit-6 .050(.001)* prescribeit-7 .034(.001)* prescribeit-8 .017(.001)* prescribeit-9 .015(.001)* prescribeit-10 .010(.001)* prescribeit-11 .012(.001)* prescribeit-12 .031(.001)* F-statistic
F(34, 1,326,323) = 12,499.10*
F(35, 1,269,179) = 71,457.70*
F(46, 578,914) = 4,364.59*
F(58, 575,687) = 22,288.70*
33
Table X (Panel B) Alternative Model Specifications: Fixed-Effect Models‡
Model X.5 Model X.6 Model X.7 Model X.8 ∆detailsit .043(.003)* .057(.005)* .055(.005)* .060(.005)* ∆detailsit-1 .031(.006)* .029(.006)* .042(.006)* ∆detailsit-2 .026(.006)* .024(.006)* .034(.006)* ∆detailsit-3 .024(.007)* .023(.007)* .014(.006)* ∆detailsit-4 .016(.006)* .015(.006)* .021(.006)* ∆detailsit-5 .002(.006) .003(.006) -.012(.006)* ∆detailsit-6 -.001(.005) -.001(.005) .001(.005) ∆samplesit .006(.004)* .006(.001)* .006(.001)* .007(.001)* ∆samplesit-1 .002(.001)* .002(.001)* .003(.001)* ∆samplesit-2 .001(.001) .001(.001) .003(.001)* ∆samplesit-3 .002(.001)* .002(.001)* .002(.001)* ∆samplesit-4 .002(.001)* .002(.001)* .003(.001)* ∆samplesit-5 .002(.001)* .002(.001)* .002(.001)* ∆samplesit-6 .001(.001) .001(.001) .001(.001)* ∆prescrbit-1
§ .022(.002)* .038(.007)* ∆prescribit-2 .023(.005)* ∆prescribit-3 .021(.004)* ∆prescribit-4 .004(.003) ∆prescribit-5 -.010(.002)* ∆prescribit-6 .003(.001) ∆competit-1 -.025(.000)* ∆competit-2 -.014(.001)* ∆competit-3 -.009(.001)* ∆competit-4 -.008(.001)* ∆competit-5 -.002(.001)* ∆competit-6 -.003(.001)* F-statistic
F(34, 1,262,153) = 274.92*
F(39, 855,580) = 144.09*
F(40, 851,773) = 140.96*
F(26, 851,267) = 134.29*
‡ Model specifications are provided in the Table 3 Legend. Results are presented as estimate (standard error). All models, except Model X, also include time-period-specific and specialty-specific intercepts. The number of observations differs across the models due to the taking of first differences, the inclusion of six or twelve lagged terms, and removing outliers. § Instrumental variable estimate utilized. * P value < 0.05
34
Table X Legend Panel A: Level Models Ignoring Physician-Specific Fixed Effect:
Model X.1: Prescribeit = α0+ β0*Detailsit + γ0*Samplesit + δ∑Τ
=1ττ *Time(τ) + κs*Specialty(s) + ηit ∑
=
11
1s
Model X.2: Prescribeit = α0+ β0*Detailsit + γ0*Samplesit + φ1*Prescribeit-1 + δ∑Τ
=1ττ *Time(τ)
+ ∑ κs*Specialty(s) + ηit =
11
1s
Model X.3: Prescribeit = α0+ βj*Detailsit-j + ∑ γj*Samplesit-j + δ∑=
12
0j =
12
0j∑
Τ
=1ττ*Time(τ)
+ ∑ κs*Specialty(s)+ηit =
11
1s
Model X.4: Prescribeit = α0+ βj*Detailsit-j + ∑ γj*Samplesit-j + φj*Prescribeit-j ∑=
12
0j =
12
0j∑
=
12
1j
+ ∑ δΤ
=1ττ*Time(τ) + κs*Specialty(s) + ηit ∑
=
11
1s
Panel B: Alternative Fixed-Effects Model Specifications:
Model X.5: ∆Prescribeit = β0*∆Detailsit + γ0*∆Samplesit + ∑Τ
=1τδτ*∆Time(τ) + κs*Specialty(s) + ηit ∑
=
11
1s
Model X.6: ∆Prescribeit = ∑ βj*∆Detailsit-j + γj*∆Samplesit-j =
6
0j∑
=
6
0j
+ ∑ δΤ
=1ττ*∆Time(τ) + κs*Specialty(s) + ηit ∑
=
11
1s
Model X.7: ∆Prescribeit = ∑ βj*∆Detailsit-j + γj*∆Samplesit-j + φ1*∆Prescribeit-1 =
6
0j∑
=
6
0j
+ ∑ δΤ
=1ττ*∆Time(τ) + κs*Specialty(s) + ηit ∑
=
11
1s
Model X.8: ∆Prescribeit = ∑ βj*∆Detailsit-j + γj*∆Samplesit-j + φj*∆Prescribeit-j =
6
0j∑
=
6
0j∑
=
6
0j
+ ∑ λj*∆Competitorit-j + ηit =
6
1j
35
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