Estimating Treatment Effects with
Observational Data using Instrumental
Variable Estimation: The Extent of
Inference
John M. Brooks, Ph.D.
Health Effectiveness Research Center (HERCe)
Colleges of Pharmacy and Public Health
University of Iowa
June 26, 2005
Health
Effectiveness
Research
Center
1
Research Goal:
• Estimate casual relationships between
"treatment" and “outcome” in
healthcare...
→
→
→
→
treatment on outcome;
behavior on outcome;
system change on behavior (e.g.
guideline implementation);
system change on outcome.
2
• Written as a linear relationship:
Y = a0 + a1• T
our goal is to obtain estimate(s) of “a1”.
• To estimate “a1” T must move or vary.
• To make inferences about “a1” the source
of the variation in T must be scrutinized
relative to your research goal.
3
• Key research design issues for isolating and
using “T” variation:
1. the manner in which the researcher collects
data; and
2. the approach to deal with “confounding
factors”
confounding factors: factors that vary both
with T and Y.
4
Research Environments and Estimation Methods
Statistical “Matching”
Techniques (Propensity Scores)
Secondary
Databases
Quasi-Experimental Designs
ANOVA
Logistic Regression
Instrumental Variables
Multiple Regression
– “Ex Post Design”
– “Risk Adjustment”
Statistical Control of
Confounding Factors
Design Control of
Confounding Factors
Weighted Regression
Techniques of Survey
Databases:
• NMES
• MEPS
Entirely Controlled
2
Experiment - 
Tests
– Randomized
Controlled Trials
Researcher-Collected
Databases
5
Sources of Treatment Variation in Health Care
1. Randomized Controlled Trials: study of patients with
a given medical condition in which treatment is
randomly assigned.
• Why randomly assign treatment to patients?
To help ensure that estimated treatment effects
result from the treatment variation and not
unmeasured confounders.
The Gold Standard
6
• Why not more Randomized Controlled Trials?
→ ethical problems once treatment is
approved
→ expensive and time-consuming
→ little motivation
→ patient sampling problems when comparing
existing treatments (so who wants to be
randomized?)
7
2. Observational Healthcare Databases Containing
Healthcare Treatment Choices:
• Secondary:
→ Claims: medical service treatment claims from
individuals with health insurance
→ Provider-Specific: databases describing the
utilization of a set of providers.
• Primary:
→ Health Care Surveys: surveys of patients or
providers detailing health
8
care utilization.
• Strengths:
→ plenty of variation in treatment choice;
→ ability to study effects of treatment across a
variety of clinical scenarios;
→ can assess treatments in practice – estimate
“effectiveness”;
→ often unobtrusively collected;
→ the power of large numbers and time.
9
• Weaknesses:
→ often data usually not collected for researcher’s
purpose (secondary);
→ patient enrollment variation;
→ confounding information may be unobserved.
-
care not covered is not observed
care not claimed is not observed
claim form limitations
nuances of illness, treatment, and patient that can’t
be recorded on claims forms
10
Is the Main Weakness with Observational Data
Unmeasured Confounders or Treatment Selection Bias?
1. Unmeasured Confounders
• Unmeasured Confounders argument:
→ homogenous treatment effect (a1 same for all
patients); and
→ unmeasured factors related to both treatment
and outcome is the source of bias.
11
• Assume true outcome relationship is:
Y = ao +
a1•T + a2•L + e
where:
Y = measure of outcome (e.g. 1 if survive to a
certain time period, 0 otherwise);
T = 1 if receive treatment, 0 otherwise; and
L = additional factor (e.g. severity, other treatments).
Goal is to estimate a1 – the effect of treatment on outcome.
12
• For Estimation Suppose:
→ L is not measured and the estimation model is:
Y = ao +
u
=
a1•T + u
where:
(a2•L + e)
→ L is related to Y (a2 ≠ 0); and
→ T and L are related (Cov(T,L) ≠ 0).
Cov(T,L) – covariance of T & L. Cov(T,L) ≠ 0 essentially
means that T & L move together.
13
• Define the ordinary least squares (ANOVA) estimate of
a1 as â1 .
→ It can be shown that under these assumptions â1 is
a biased estimate of a1 through its expected value:
E[aˆ1 ] = a1 + Cov(T,L)•a2
→ Also note that E[aˆ1 ] will equal a1 if either:
-- Cov(T,L) = 0; or
-- a2 = 0.
14
• Suppose theory about the unmeasured variable “L”
suggests:
→ “a2 < 0” (patients with higher severity are less likely
to survive).
→ Cov(T,L) > 0 (treated patients are generally more
severe).
• Plug in “signs” into our expected value formula to find:
E [ aˆ1 ]  a1  ()( )
( )
→
E[aˆ1 ]
<
a1.
15
• Problem with the Unmeasured Confounders argument
to describe bias in observational data:
→ No theoretical foundation linking treatments to
unmeasured factors....
Why is Cov(T,L) ≠ 0?
→ In the example above, if treatment effect (a1) is the
same for all patients, why would Cov(T,L) > 0?
Perhaps patients getting treated:
-- live in areas with high/low poverty;
-- live in areas with more pollution; or
-- also tend to get other unmeasured treatments.
16
2. Treatment Selection Bias (the gestalt underlying most
negative reviewer’s comments)
• Treatment Selection Bias argument:
→ Heterogeneous treatment effect -- Cov(T,L) is a
reflection of decision-maker’s beliefs about the
treatment effectiveness across patients related
to unmeasured factors “L”.
→ “Bias” comes from unmeasured factors (L) being
related to the treatment choice and outcome.
→ Researcher must address both bias and ability
to generalize (to whom do the results apply?).
17
• Assume true outcome relationship is:
Y = bo + (b1•L) •T + b2•L + e
where:
Y
= measure of outcome (e.g. 1 if survive to a
certain time period, 0 otherwise);
T
= 1 if receive treatment, 0 otherwise;
L
= unmeasured factor (e.g. severity, other
treatment);
b2
= the direct effect of L on Y; and
(b1•L) = effect of T on Y that depends on L.
18
→ L is now related to T through theory linking "treatment
choice" to the decision-maker’s expectations of
treatment benefits across patients with different “L”.
T = co + c1•L + c2•W +
v
where:
T = 1 if receive treatment, 0 otherwise;
L = unmeasured factor (e.g. severity, other
treatment) affecting treatment choice through
expected treatment effectiveness; and
W = other factors affecting treatment choice.
If decision makers use L in treatment
decisions, c1 ≠ 0 and Cov(T,L) ≠ 0.
19
• Ultimate goal should be to estimate (b1•L) – the
effect of treatment T on outcome Y across levels
of L.
• For estimation suppose:
→ L is not measured and it is wrongly assumed
by the researcher that the effect of T is
homogenous, and the estimation model is:
Y = ao +
a1•T + u
where:
u = f(L,T, e, b1,b2)
20
• Define the ordinary least squares (ANOVA) estimate of
a1 as â1 .
→ It can be shown that the expected value of â1 is:
E â   b  E [ L |T 1 ]  c  b
1
1
1
2
→ If b2 = 0 (L has no direct effect on Y) or c1 = 0 (no
selection based on L), then E â1  becomes:
E â   b  E [ L |T 1 ]
1
1
Yields an average estimate of the treatment effect for
“the treated” in the sample. Result can be generalized
21
only to those with L similar to those treated.
• How does c1 • b2 affect this estimate?
→ Assume that L is unmeasured illness severity
and that higher L means more severe illness.
→ Higher L lowers survival which implies b2 < 0.
→ If treatment benefit is less for more severe cases
(e.g. surgery for heart attacks) then:
b  0  c  0  c  b      0
1
1
benefit falls
with higher
less treatment
in more
severity
severe cases
1
2
Estimate of the effect of the treatment on the treated
22
will be biased high.
→ If treatment benefit is greater for more severe cases
(e.g. antibiotics for otitis media) then:
b  0  c  0  c  b      0
1
1
1
2
benefit increases more treatment
with higher
in more
severity
severe cases
Estimate of the effect of the treatment on the treated
will be biased low.
23
• So what do we have here?
→ Observational data contains treatment variation.
→ If treatment benefits are heterogeneous the best you
can get is an estimate of the treatment effect on the
treated (Does this address the benefits from
expanding treatments?).
→ Treatment selection may be based on unmeasured
factors related to both treatment effectiveness and
outcomes.
→ If unmeasured factors affecting selection also
effect outcomes directly, estimate will be biased.
Do we have any alternatives?
24
Instrumental Variables (IV) Estimation and “Subset B”
• IV estimation offers consistent estimates for a subset of
patients (McClellan, Newhouse 1993):
Marginal Patients: patients whose treatment choices vary
with measured factors called instruments
that do not directly affect outcomes.
• McClellan and Newhouse argued that estimates of treatment
effects for Marginal Patients are useful.
→ Estimates may be more suitable than RCT estimates to
address the question of whether existing treatment rates
should change.
25
• Where do Marginal Patients come from?
Distribution of Patients by Prior Assessment of
the Certainty of Treatment Benefit
A
0%
More certainty
about treatment
benefits
B
50%
C
100%
Less certainty
about treatment
benefits
A = subset of patients all providers agree to treat.
C = subset of patients all providers agree not to treat.
B = subset of patients whose treatment choice is
situation/provider dependent.
26
• Patients in Subset B are interesting because:
→ the “best” treatment choice (treat or don’t treat) is
least certain;
→ treatment or no-treatment for a patient in this subset
is not considered bad medicine – the “art” of
medicine;
→ the possibility of gaining new RCT evidence for
patients in this subset is remote (ethics, motivation);
→ McClellan et al. 1994 argue that (1) policy
interventions and (2) non-clinical factors (e.g.
provider access, market pressures) affect mainly the
treatment choices of patients in this subset.
27
• Size and location of Subset B varies with clinical scenario.
 treatment with little consensus (e.g. aggressive treatment
for early-stage prostate cancer):
A
B
0%
50%
More
Certainty
C
100%
Less
Certainty
 off-label use for new treatment (e.g. new anti-cancer
drugs used in non-tested cancer populations):
B
0%
More
Certainty
C
50%
100%
Less
Certainty
28
• Changes in the underlying population definition will affect
the location of Subset B.
 aggressive treatment for early-stage prostate cancer for
50-60 year-olds with no comorbidities:
A
0%
B
50%
C
100%
More
Certainty
Less
Certainty
 aggressive treatment for early-stage prostate cancer for
70-80 year-olds with one comorbidity:
A
0%
More
Certainty
C
B
50%
100%
Less
Certainty
29
• IV estimation involves:
1. Finding measured variables or “instruments” (Z) that:
a. are related to the possibility of a patient receiving
treatment (cov(T,Z) ≠ 0); and
b. are assumed (through theory) unrelated directly to Y
or to unmeasured confounding variables (cov(Z,L) = 0).
The theoretical basis for “Z” variables should come from
a model of treatment choice – the “W” variables in:
T = co + c1•L + c2•W +
v
where:
W = other factors affecting treatment choice.
30
• IV estimation involves con’t:
2. Grouping patients using values of the
“instrument”.
3. Estimate treatment effects for marginal
patients by exploiting treatment rate
differences across patient groups.
Local Average Treatment Effect -(Imbens & Angrist 1994)
31
• For example, if an instrument divides patients into two
groups, a simple IV estimate can be found by calculating:
1. the overall treatment rate in each group (ti = treatment
rate in group “i”); and
2.
the overall outcome rate in each group (yi = outcome
rate in group “i”); and estimate:
aˆ1IV 
difference in outcome rate
y1  y 2

difference in treatment rate
t1  t 2
where:
aˆ1IV
= average treatment effect for the “marginal patients”
specific to the instrument used in the analysis –
only those patients whose treatment choices were
affected by the instrument who must have come
32
from Subset B.
• Hypothetical Treatment Choices Across Patients
Grouped by Access to Providers Required for Treatment
Patient Group Closer to Providers Required for Treatment:
treated
A
B M
C
0%
More Certainty
100%
Less Certainty
Patient Group Further From Providers Required for Treatment:
treated
A
0%
More Certainty
M
B M
50% 60%
C
100%
Less Certainty
= patients within Subset B whose treatment choices
are affected by the instrument – the Marginal
Patients for that instrument.
33
• We have treatment rates for each group:
Closer Group Treatment Rate: .60
Further Group Treatment Rate: .50
Suppose we also measured “cure” rates in both groups:
Closer Group Cure Rate: .40
Further Group Cure Rate: .38
• Four numbers lead to the following IV estimate:
.40 .38
.02
â 

 .2
.6  . 5
.1
1IV
34
• Strict Interpretation:
→ If the treatment rate in the Further Group was increased .01
percentage point (e.g. .50 to .51) by increasing treatment
for the M patients in the Further Group, the Cure rate in the
Further Group would increase .002 (.01 • .2) – from .38 to
.382.
• Stretched “Policy-Relevant” Interpretation (McClellan et al.
1994)
→ A behavioral intervention that increases the overall
treatment rate by .01 percentage point (e.g. .55 to .56)
would lead to an increase in the cure rate of .002 (.01 • .2).
35
• Stretched interpretation assumes that the treatment effect
for patients in Subset B is fairly homogenous and an IV
estimate from a single instrument can be generalized to all
patients in Subset B.
• Stretched interpretation may not be accurate if treatment
effects are heterogeneous within Subset B and different
instruments affect treatment choices from different patients
within Subset B.
→ Results from a single instrument may still be more
appropriate than assuming RCT results apply to Subset B.
→ Ability to generalize results may increase if more than one
instrument is used in an IV analysis.
36
• IV qualifiers to remember:
→ second property of IV variables (cov(Z,L) = 0) is
forever an assumption (unless more data are
obtained);
→ unmeasured but correlated treatments may still bias
estimated treatment benefits; and
→ ability to generalize is limited.
Researchers should fully qualify their IV estimates –
don't oversell.
37
Hypothetical Example to Demonstrate “4-Number” Result
Suppose:
• 2100 children with Otitis Media (OM) in a population.
• Two treatment possibilities:
1.
2.
antibiotics;
watchful waiting.
• The patients in our sample are in one of three severity
types “low”, “medium”, and “high”
• Severity type is observed by the provider/patient but is
not observed by the researcher.
38
• The 2100 patients are distributed across severity type in the
following manner:
number of patients
High
800
severity type
Medium
800
Low
500
• The actual underlying cure rates for each severity type by
treatment are:
treatment
antibiotics
watchful waiting
High
.95
.80
severity type
Medium
.97
.90
Low
.98
.98
39
→ Higher severity means a lower the cure rate in general
(b2 < 0).
→ Treatment effects are heterogeneous and antibiotics have
a higher curative effect in more severe patients and offer
no advantage to the less severe (b1 > 0).
→ All providers have inclination that antibiotics work well in
the "high" severity patients; have little effect on the "low"
severity patients; but the effect in the "medium" type is
unknown.
→ Leads to treatment selection bias...the more severe kids
are treated (c1 > 0) and more severe kids are less likely
cured (b2 < 0).
40
Potential Methods to Get Treatment Variation for Analysis:
1. Randomize Patients Into Treatments -- ANOVA
2. Providers Assign Treatments -- ANOVA
3. Instrumental Variable Grouping
41
1. Randomize Patients Across Population – ANOVA.
Patient Treatment Assignments After Randomization
by Severity Type
patient groups
antibiotics
watchful waiting
severity type
High
Medium
400
400
400
400
Low
250
250
42
Expected average cure rates for each group:
400
400
250
Antibiotic Cure Rate 
.95 
.97 
.98 .965
1050
1050
1050
400
400
250
W .W .Cure Rate 
.80 
.90 
.98 .881
1050
1050
1050
• Unbiased average antibiotic treatment effect for the
entire population (.965-.881 = .084), but
• Estimate will vary with the average severity in the
population...E[L|T=1].
• To whom does it apply? A patient randomly chosen
43
from an urn? Are patients chosen from urns?
2.
Providers Assign Treatments -- ANOVA
If providers follow “inclinations”, we may end up with
something like:
Number of Patients Assigned by Providers to Each
Treatment Group by Severity Type
patient group
antibiotics
watchful waiting
High
800
0
severity type
Medium
400
400
Low
0
500
44
Expected average cure rates for each group:
800
400
0
Antibiotic Cure Rate 
.95 
.97 
.98 .957
1200
1200
1200
0
400
500
W .W .Cure Rate 
.80 
.90 
.98 .944
900
900
900
• For this population the average treatment effect is on the
treated (800/1200*.15 + 400/1200*.07=.123).
• We
find a biased low estimate of the antibiotic treatment
effect for the average treated patient (.957 - .944 = .013 < .123).
• “Biased low” follows our theory as...
45
3. Instrumental Variable Grouping – Further assume:
a.
Information is available to the researcher to
approximate distances from patients to providers
• address of patient
• supply of providers in area around patients
b. Evidence suggests that patients in areas with more
physicians per capita have a higher probability of being
treated with antibiotics for their OM than patients in
areas with fewer physicians per capita.
46
If “b” is true, divide 2100 patients into two groups based on
the physicians per capita in the area around their home:
Group 1: the group of patients living in areas with a higher
number of physicians per capita.
Group 2: the group of patients living in areas with a lower
number of physicians per capita.
47
Using our assumptions, does this grouping qualify as an
instrument?
1. Doc supply related to treatment? Yes, if patients tend to go to
the closest provider for
treatment.
If true, and providers follow inclinations we may see treatment
patterns something like:
Patient Treatment Assignments by Severity Type
patient
group
Group 1
High
100% antibiotics
Group 2
100% antibiotics
severity type
Medium
80% antibiotics
20% W.W.
30% antibiotics
70% W.W.
Low
100% W.W.
100% W.W.
48
2. Is grouping related to unmeasured confounding variables
(e.g. severity)? Related to severity only if parents chose
residences in expectation of the severity of a future acute
condition.
If not related to severity, we assume equivalent severity
distributions across groups:
Number of Patients in Each Group by Severity Type
patient group
Group 1
Group 2
High
400
400
severity type
Medium
400
400
Low
250
250
49
Expected average estimated cure rates for these groups:
Group 1 Cure Rate 
400
320
80
250
.95 
.97 
.90 
.98 .959428
1050
1050
1050
1050
Group 2 Cure Rate 
400
120
280
250
.95 
.97 
.90 
.98 .946092
1050
1050
1050
1050
Well, (.959428 - .946092) = .013336 doesn't appear to reveal
much of anything…!
50
Now look at the antibiotic treatment rate in each group:
720/1050 = .68571 in Group 1
520/1050 = .4952381 in Group 2
These differences also don't look very informative….
The IV change in the cure rates resulting from a one unit
increase in the drug treatment rate equals:
aˆ1IV
.959428  .946092
.013336


 .07
.68571 .4952381
.190471905
• This estimate is the average difference in the antibiotic cure
rate for the marginal or in this example the “Medium”
severity patients.
51
• Remember the actual “unknown” cure rates for each
group by treatment are:
treatment
antibiotics
watchful waiting
High
.95
.80
severity type
Medium
.97
.90
.07
Low
.98
.98
• This estimate was found using only measured treatment
rates and outcome rates across “groups” that are
defined by the instruments.
• Which of the estimates above is the most important for
policy-makers wondering about over/underutilization of
a treatment?
52
IV Brass Tacks
• Where do instruments come from?
→ Theory on what motivated choices, not theory on
how choices can be motivated.
→ Observed differences in:
-- guideline implementation (timing/interpretation)
-- product approval rules across payers
-- reimbursement differences across payers/geography
-- area provider “treatment signatures”
-- geographic access to relevant providers
-- provider market structure/competition
→ Generally, “Natural Experiments” (Angrist and Krueger,
2001)
53
• General IV Estimation Model
Treatment Choice Equation (1st stage):
T  c  c  X  c Z  v  c L 
i
0
2
i
3
i
Outcome Equation (2nd stage):
i
1
i
Yi  a0  a1  Tˆi  a2  X i  ei  a3  Li

Yi = 1 if health outcome occurs, 0 otherwise;
Xi = measured patient clinical characteristics;
Ti = 1 if patient received treatment, 0 otherwise;
Tˆi = predicted treatment from 1st stage;
Zi = a set of binary variables grouping patients based on
values of instrumental variables (from W); and
Li = unmeasured confounding variables assumed related
to both Y and T but not Z.
The only variation in T used to estimate a1 comes from Z.
54
• Define the IV estimate of a1 as
aˆ1IV
.
→ It can be shown that the expected value of aˆ1IV is:
E â
1 IV
  b  E [ L |T ( Z )]
1
Yields an average estimate of the treatment effect for
the set of patients whose treatment choices were
dependent on their value of Z.
55
→ The estimate of a1 can only be definitively generalized
to the patients whose treatment choices were affected
by Z (Angrist, Imbens, Rubin 1996).
→ F-test of whether the parameters within c3 are
simultaneously equal to zero provides a test of the
first instrumental variable criterion:
Finding measured variables or “instruments” (Z) that:
a. are related to the possibility of a patient receiving
treatment (cov(T,Z) ≠ 0)
56
→ Model can be estimated via:
-- Two-Stage Least Squares (2SLS) – PROC
SYSLIN in SAS.
-- Bivariate Probit – BIPROBIT function in STATA.
-- Two-Stage Replacement (e.g. Beenstock &
Rahav, 2002).
→ 2SLS offers consistent estimates that are
asymptotically normal with the fewest assumptions
(Angrist 2001).
-- essentially regressing group-level outcome rate
changes on group-level treatment rate changes.
57
• How many groups?
→ Z can be specified as continuous variables, but results
are then conditional on this assumption and are less
interpretable.
→ Creating many groups from an instrument (more binary
variables in Z) uses more information and yields a
weighted average of many two-group comparisons, e.g.
-- low/high groups using the median of the instrument
VS
-- low/med low/med high/high groups using the
quartiles of the instrument.
→ Too many groups may introduce bias.
→ Best to report estimates for several grouping strategies.
58
Effect of Dialysis Center ProfitStatus on Patient Survival: An
Instrumental Variables Approach
Brooks, Irwin, Pendergast, Chrischilles, Flanigan,
Hunsicker
59
Introduction
In a meta-analysis of observational studies,
Devereaux et al (1) found that patient survival at
for-profit dialysis centers was poorer than nonprofit centers.
Objective
Compare estimates of the effect of dialysis center
profit status on patient survival using riskadjustment and IV estimation.
60
Sample
• N =
101,669 incident ESRD patients from United States
Renal Data System (USRDS) from 1996-1999 that:
-- were between 67 and 100 years old at dialysis initiation;
-- had hemodialysis as initial modality;
-- obtained dialysis in a non-government dialysis facility;
-- had complete information on all model variables;
-- zip codes linked to 1990 census data.
Key Variable Definitions
• Outcome: one-year survival after dialysis initiation = 1,
0 otherwise.
• Treatment Setting: patient initiated dialysis in a for-profit
dialysis center = 1, 0 otherwise.
61
Instrumental Variable Strategy
• Followed McClellan et al. (1994) and grouped patients
based on Differential Distance (DD) to various hospital
classifications:
DD
=
(DFP - DNP)
where
DFP = distance from patient residence to the nearest for
profit dialysis center; and
DNP = distance from patient residence to the nearest
non-profit dialysis center.
• Assessed whether IV estimates were robust to the
number of patient groups defined using differential
distance.
62
Percent Initial For-Profit and Number of Comorbidities
by Patient Differential Distance
5
0.8
% for-profit
4
0.6
3
0.4
0.2
2
Average number of comorbidities
% for-profit
comorbidities
1.0
0.0
for-profit closer
not for-profit closer
1
-100
-50
0
50
100
Miles a not for-profit is closer
63
Table 1: Attributes of Dialysis Patient Groups, 1996-1999
Patient
Treatment Setting
Characteristics For-Profit Non-Profit
For Profit %
100
0
White %
70.6
73.3**
Black %
23.5
20.0**
Cardiac Failure % 42.6
44.2**
Diabetes %
45.1
41.3**
CerebroVasc Dis% 11.9
12.5**
Isch Heart Disc % 32.1
36.1**
AMI
11.6
13.2**
Reside in:a
High Hlth State % 61.2
47.4**
Med Hlth State % 16.4
40.3**
Low Hlth State % 22.4
12.3**
Number
73,480
30,678
Differential Distance (DD)
Patient Closer to:
For-Profit
Non-Profit
92.8
48.1**
74.9
67.9**
19.8
25.1**
43.1
43.1
44.8
43.1**
12.0
12.1
33.5
33.1
12.2
12.0
61.4
13.7
24.9
52,443
52.9**
33.3
13.9**
51,715
a.Subramanian, S, Kawacki I, et al. (2001). “Does the state you live in make a difference? A multilevel analysis of
self-rated health in the US.” Social Science & Medicine 53(1): 9-19.
**,* statistically significant at the .01 and .05 levels, respectively
64
“Marginal” End Stage Renal Disease Patients,
1996-1999
48.1%
92.8%
M
0%
More Likely
to For-Profit
50%
100%
Less Likely
to For-Profit
M = patients whose dialysis center choice is dependent on
the relative distance to for-profit and non-profit dialysis
centers – Marginal Patients.
65
Table 2: F-Statistics Testing Factors in Center Choice
Model are Related to the Use of For-Profit
Dialysis Facilities, 1996-1999.
Factora
Differential Distance (instrument)
Year
Gender
Age
Race
Comorbidity
Previous Healthcare Use
State of Residence
Distance to Nearest Center
Area Socioeconomic Status
Partial F-Statistics .
2150.53**
59.53**
5.81**
7.29**
6.26**
8.55**
2.63*
212.00**
75.41**
21.83**
a. specified using binary variables reflecting differences in respective characteristic.
Differential distance was used to group patients into 20 separate groups.
**,* statistically significant at the .01 and .05 levels, respectively
66
Table 3: 2SLS/IV and Ordinary Least Squares (OLS) Estimates of the
Effect of Initial For-Profit Initial Dialysis Provider Relative to a
Non-Profit Provider on 1-Year Patient Survival
Estimation Model
Number of Instrument
and Specification
Groups Specified
OLS no covariates
na
OLS Devereaux covariatesa
na
OLS Devereuax covariates plusb na
2SLS/IVb
2
2SLS/IVb
5
2SLS/IVb
10
2SLS/IVb
20
2SLS/IVb
40
Estimate (P-value)
-0.0031c (0.3450)
-0.0122c (<.0001)
-0.0071c (0.0511)
0.0009 (0.9264)
0.0025 (0.7373)
-0.00004 (0.9953)
-0.0002 (0.9823)
0.0006 (0.9349)
a. Factors consistently controlled for in the studies within the Devereaux meta-analysis – age,
gender, race, comorbidities.
b. Factors consistently controlled for in the studies within the Devereaux meta-analysis – age,
gender, race, comorbidities, plus dialysis year, state of residence, previous healthcare utilization,
provider access (distance to nearest dialysis center), socioeconomic status (patient zip percent
rural, percent poverty, and per capita income).
c. Logistic regression estimates were consistent in both magnitude and statistical significance.
67
OLS estimates were reported because their interpretation is more consistent with IV estimates.
Summary
• The foundation of IV estimation is theory that suggests
instruments – what factors motivated treatment choices.
• Ability to generalize is limited, but IV estimates offer a
more natural estimate of the effects of rate changes than
RCT estimates.
• Estimates can vary by sample and instrument used.
• Estimates are conditional on the truth (and acceptance)
of a known identification restriction. The source of the
treatment variation is known. The relationship between
this variation source and unmeasured confounders can
be debated.
68
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