Project Design Document

1901-Project-Design-Document-AHS.pdf

2021 American Housing Survey (AHS)

Project Design Document

OMB: 2528-0017

⚠️ Notice: This form may be outdated. More recent filings and information on OMB 2528-0017 can be found here:

2023-01-06 - Revision of a currently approved collection

Document [pdf]

Download: pdf | pdf

Project Design
Project title: Using Incentives to Reduce Nonresponse Bias in the American Housing
Survey (AHS)
Project code: 1901

1 Project Objectives
The American Housing Survey (AHS) is a biannual, longitudinal survey of housing units designed by the U.S. Department of Housing and Urban Development and administered by the U.S. Census Bureau. The sample of housing units is
drawn from residential units in the United States and is designed to provide statistics that represent both the country
as a whole and its largest metropolitan areas.
As with many federal surveys, the AHS has experienced declining response rates, requiring increasing amounts of time
and effort to reach the 80 percent response rate preferred by the Ofﬁce of Management and Budget. In particular,
response rates have declined from approximately 85 percent in the 2015 wave to 80.4 percent in the 2017 wave to
73.3 percent in the 2019 wave.1
In this project, we distinguish between nonresponse bias, on the one hand, and survey representativeness, on the other
hand. Nonresponse bias is a divergence between a population quantity of key interest—such as the true proportion of
U.S. adults living in severely inadequate housing—and its sample estimate, which arises due to systematic differences
between those who do and do not respond to a survey.2 In theory, it is possible to adjust survey estimates to account
for differential nonresponse so that sample estimates converge to population quantities, and bias is removed. To account for potential nonresponse bias, the AHS calculates a nonresponse adjustment factor (NRAF) that reweights for
nonresponse within cells deﬁned by metropolitan area, type of housing unit, block group median income, and arealevel rural/urban status. In principle, adjustments such as this, along with raking, should reduce or even remove the
inferential threats posed by nonresponse bias. However, there is no guarantee that the model used for bias-adjusted
estimates contains all the information it needs. Moreover, the weights used in such bias adjustment schemes typically
increase variance in estimates: they essentially require units in grid cells with a lot of missingness to “represent” more
unobserved units than those in grid cells with less missingness.
Furthermore, our preliminary analyses leave open the possibility that the raking and nonresponse adjustment factors
currently employed to reweight AHS estimates do not ensure convergence with population quantities. For example, a
key outcome the AHS measures is housing inadequacy. Among units where an interview was successfully conducted
during the 2015 wave of the AHS, some dropped out due to nonresponse in 2017. Reweighted estimates suggest
12 percent of those who stayed in the panel in 2015 and 2017 had problems with rodents. Looking at those housing
units that appeared in 2015 only to drop out in 2017, however, only 9 percent had problems with rodents—in other
words, a key measure of housing quality appears correlated with differential panel attrition. In a separate memo on
nonresponse bias in prior rounds of the AHS (see attached), we found numerous systematic patterns in panel attrition
whose statistical and substantive signiﬁcance persists in spite of weighting meant to account for nonresponse bias.
We found the AHS bias-adjusted estimate of the proportion of householders in the U.S. who own their home outright
1
The response rates for the 2015 and 2017 waves are taken from the AHS public methodology reports. The response rate for the 2019 wave
is taken from our analysis of the IUF with the below restrictions to the national sample and excluding the bridge sample, with values based on
the coding responders as STATUS == 1, 2, or 3 (n = 63, 186) and nonresponders as STATUS == 4 (n = 22, 965). These may differ from those
in the published methodology report if there are different inclusion criteria for the published rates to remove ineligible households.
2
In other words, it is a correlation between the propensity to respond to the survey and a key outcome of interest.

http://oes.gsa.gov

(without a mortgage or loan) in 2015 is seven percentage points lower than the corresponding proportion in the 2010
Decennial census count.3 Attributing such divergence to nonresponse bias with complete certainty is a challenging
task since, by deﬁnition, we cannot measure the outcomes of those who do not respond. However, the many pieces
of evidence presented in the nonresponse bias memo suggest that, in addition to adjusting sample estimates on the
backend, improving sample composition on the frontend would increase their accuracy.
The question of survey representativeness relates closely to that of nonresponse bias: it describes systematic differences between sampled units who do and do not respond to the survey on demographic and administrative variables,
rather than on key outcomes. While demographic and administrative measures may often be of secondary importance
to decision-making, they help to understand the extent to which missingness due to nonresponse is random or systematic. In our separate memo, we ﬁnd responders and non-responders differ systematically on a range of attributes, both
within and between waves of the survey. These divergences are important to understand for at least three reasons:
1) demographic and administrative variables often deﬁne subgroups among whom key outcomes are estimated (e.g.,
the rate of housing inadequacy in rural versus urban areas); 2) as described above, these variables are employed to
conduct reweighting as they are often the only ones available for nonresponders; 3) demographic and administrative
variables provide a window onto nonresponse bias as they are correlated with key outcomes. See on this last point, for
example, Figure 1, which illustrates that panel attrition in 2017 is predicted by the age of the householder interviewed
in 2015, and that householder age is also correlated strongly with measures of housing adequacy. As such, improving
the representation of units with young householders may reduce bias in estimates of housing adequacy.
In Adequate Housing
in 2015

Refused Survey
in 2017
16.0%
14.0%

95.00%

N Interviewed
in 2015

12.0%
93.00%

500
1000

10.0%

1500
8.0%

91.00%

2000

6.0%
20

Age of householder interviewed in 2015
Figure 1: Units with young householders in 2015 were a) less likely to be adequate housing in 2015 and b) more likely to drop out
of the panel due to refusal in 2017. Points represent reweighted estimates of proportions for different ages, size corresponds to
number of respondents in 2015.

The purpose of this project is to determine whether and how the provision of cash incentives prior to contact with
Census Bureau staff can achieve two related goals: reducing nonresponse bias in (adjusted and unadjusted) sample
estimates and increasing representativeness of the sample. The project aims to yield insights about the optimal allocation of a ﬁxed incentive budget, both in terms of how much to spend on potential respondents and which respondents
to target. We will also investigate effects of incentives on the effort required to obtain interviews among successful
and unsuccessful interview attempts, by measuring reduction in the number of contact attempts.
3

Signiﬁcant at the α = .01 level, using replicate weights to estimate variance.

http://oes.gsa.gov

2 Intervention Design
Our intervention consists of sending cash to potential respondents sampled as part of the Integrated National Sample of the 2021 American Housing Survey. The cash is delivered inside an envelope containing a letter reminding the
potential respondent about the survey. This letter is sent both to treatment and to control respondents, albeit with a
slight wording change that mentions the incentive in the treatment letter and not in the control (see appendix for both
letters). The timeline is depicted on Figure 2.

Figure 2: Intervention timeline.

Given the risks survey nonresponse raises—sample size reduction and possible bias—it is not surprising that a large
literature has developed seeking to understand and reduce nonresponse. This project builds on a branch of this literature demonstrating the effectiveness of cash incentives at increasing response rates. We focus here on “noncontigent”
and “nondiscretionary” cash incentives (Jackson, McPhee, and Lavrakas 2020). The cash incentives are noncontingent
because they are provided to respondents in advance of the survey rather than only provided upon survey completion.4 Second, the presence and magnitude of the incentive is nondiscretionary because it is determined centrally for
all survey respondents, rather than at the discretion of individual ﬁeld staff for particular respondents.
In the context of the AHS, three questions are of central interest:
1. What contributes to survey nonresponse?
2. Given those contributors, to whom should surveyors allocate incentives in order to reduce nonresponse bias?
3. What magnitude of incentives should surveyors allocate?
We provide a brief overview of existing research in each area, and discuss gaps the present experiment aims to ﬁll.

2.1 What contributes to survey nonresponse?
Groves, Singer, and Corning (2000) suggests that a lack of awareness or salience may contribute to nonresponse, while
Hidi and Renninger (2006) and Ariely, Bracha, and Meier (2009) focus on lack of interest and motivation as behavioral
explanations for nonresponse. In the context of a survey ﬁelded by the federal government, distrust of government
may also play a role. Certain groups may also have schedules and behavioral patterns that make them harder to contact
than other groups. Our analyses suggest, for example, that units in the AHS with younger householders interviewed
in 2015 were more likely to refuse in 2017.
In addition to household characteristics, the mode of surveying also appears to matter. Laurie and Lynn (2008) note
4

These are often described as “unconditional” incentives.

http://oes.gsa.gov

that incentives are more effective in non-in-person surveys (2009: 207), possibly because of the already-high response
rates of in-person surveys. In the context of the AHS, the rate of telephonic surveying has increased substantially: from
27 percent in 2015, 30 percent in 2017, to 37 percent in 2019. This trend may thus have provided conditions that are
particularly suited to the use of incentives, though it should be noted that the evidence on how survey mode inﬂuences
incentive effectiveness is mixed.

2.2 To whom should surveyors provide incentives?
A large body of research has found that incentives generally work to improve response rates, regardless of a particular
household’s constraints and barriers to survey participation. In a meta-analysis of 49 studies, noncontingent ﬁnancial
incentives were predicted to increase response rates from an average of a rate of 85 percent to an average of 92 percent (Edwards et al. 2002). In a meta-analysis of over 20 years of articles, Mercer et al. (2015) ﬁnd that the largest
marginal gains occur between $0 and $1, and taper off considerably after $2 (2015:122).
Yet the bulk of the studies in these meta-analyses use the following procedure:
• Decide on an incentive amount to vary (e.g., $1 versus $5, with Mercer et al. (2015)’s review of studies showing
incentives that vary between $0 and $50)
• Randomly assign sampled units to receive different incentive amounts
While this procedure allows researchers to assess the impact of different incentive magnitudes, it ignores the fact
that households differ in three ways. First is the household’s likelihood of nonresponse. Second, among the pool of
households with a low likelihood of response, is the extent to which that household’s nonresponse contributes to bias.
Third, among the pool of households with both a low likelihood of response and a high potential for that nonresponse
to contribute to bias, is the extent to which that household is likely to be impacted by incentives. A growing set of
literature seeks to: (1) identify these three groups, and (2) test approaches that target incentives on the basis of group
membership.
Researchers afﬁliated with the National Center for Educational Statistics (NCES) have explored these approaches with
various surveys. Crissey, Christopher, and Socha (2015), focusing on the 2013 update to the High School Longitudinal
Study (HSLS) and the 2014 follow up to the Beginning Postsecondary Students Longitudinal Study 2012 (BPS), estimate what they call “importance scores.” The importance scores are a function of two components. First is a propensity model for nonresponse, estimated using paradata prior to the survey collection. Second is what the authors call a
“bias-likelihood score,” or the extent to which that nonresponse will contribute to bias. The authors estimate this score
during data collection by ﬁnding the Mahalanobis distance along various attributes between (1) nonrespondents and
(2) those that have responded thus far. The importance score is a dual function of these two inputs.
Selecting respondents with the highest importance scores, the researchers randomly allocated the magnitude of incentive promised to survey respondents if they completed the survey (contingent incentive).5 The study introduces
an important conceptual approach to targeting—ﬁrst, that incentives can be targeted to a subset of respondents and
second, that researchers should take into account both response propensities and contributions to bias when selecting that subset. However, by giving incentives to all high importance respondents, it does not causally test whether
targeting represents an improvement over randomly allocated incentives—the use of targeting as such is not evaluated. Similarly, other studies investigate different ways of operationalizing whom to target with incentives—for instance, Link and Burks (2013) compare response propensities estimated using different types of variables available in
address-based sampling; Coffey and Zotti (2015) combine response propensities with sampling weights to ﬁnd “highly
inﬂuential” cases—but do not experimentally compare the effectiveness of targeting to the effectiveness of randomlyprovided incentives. Such a comparison is crucial, however, in evaluating the effectiveness of targeting.
5

The authors examine a different type of incentive—contingent or promised incentives—than the present study. With that in mind, they ﬁnd
no improvements in response rates or bias from a promise of $25 relative to $0, but a signiﬁcant improvement in both response rates and bias
from a promise of $45 compared to $25.

http://oes.gsa.gov

The most similar approach to ours is Jackson, McPhee, and Lavrakas (2020), which estimates response propensities
and uses these to target incentives to complete a screener for the National Household Education Survey (NHES).6 As in
our proposed design, Jackson, McPhee, and Lavrakas (2020) randomly divides potential respondents into a group that
receives incentives independent of their propensity or one in which propensities determine incentive receipt. Speciﬁcally, the conditions are:
1. For the group assigned to propensity-independent incentives, respondents randomly receive either a $2 noncontingent incentive or a $5 noncontingent incentive along with their screener;
2. For the group assigned to targeted incentives, low propensity cases received $10, medium propensity cases
received $5, medium-high propensity cases received $2, and very high propensity cases received $0.
Jackson, McPhee, and Lavrakas (2020) represents an important step forward for research on targeted incentives.
However, its design has a fundamental drawback: the only group in which respondents receive no incentives is the
targeted group. Thus, the effect of targeting is confounded with the effect of receiving no incentives. Unsurprisingly,
giving high-propensity respondents $0 (in group 2) versus $2 or $5 (in group 1) decreases the response rate substantially. Thus, the study does not provide a good test of the targeting mechanism per se because it confounds targeting
with the lack of incentives. Furthermore, predicting response based on demographic variables alone is notoriously
difﬁcult. In the context of the AHS, we are able to leverage previous wave response patterns to make more accurate
predictions of future behavior.
An additional point raised in Jackson, McPhee, and Lavrakas (2020) is that different incentive amounts may produce
different kinds of responses as a function of predicted response propensities. However, because the varying incentive
amounts are not randomized across different propensities, their study leaves this question largely unanswered.

2.3 What is the right incentive amount?
An early ﬁnding in the literature on incentives is that, while response rates increase as the incentive amount increases,
they do so at a decreasing rate (Armstrong (1975)). In a large meta-analysis of the effect of incentive amounts on
response rates, Mercer et al. (2015) showed that 1) the type of incentive and survey mode appeared to matter for the
dose-response curve (see Figure 3 for their in-person dose-response curve); and 2) that a relative paucity of data on
varying amounts in the context of mixed-mode, panel surveys such as the AHS made generalizing to those contexts
based on extant literature difﬁcult. Understanding where the inﬂection point lies in the AHS survey sample will help
to determine whether a ﬂat $5 incentive, as is used in the NHES, makes sense, or whether differing amounts need to
be used among different subgroups.

Figure 3: Dose-response effect of incentives on response rate in in-person surveys using noncontingent incentives, reproduced
from the Mercer et al. (2015) meta-analysis.

Our study plans to randomize respondents to one of four amounts: $0, $1, $5, and $10. The $5 dollar amount is chosen
6
The authors use a two-stage approach. First, they use a conditional inference tree for variable selection. Then, they use logistic regression
with the selected variables.

http://oes.gsa.gov

Improvement in response
vs. no incentive

as it corresponds to amounts in similar surveys such as the NHES. Figure 4 demonstrates examples of the response
curves we might ﬁnd. The dotted curves illustrate unobservable dose-response curves, while the solid curves and
points show estimable quantities that the design can elicit.

0.6

●

●
●

●

0 1 2

0.4

0.2

0.0

●

Dollar amount of incentive
Hypothetical
Respondent Types

●

Low−cost

●

Medium−cost

●

High−cost

Figure 4: Possible dose-response curves and estimable linear relationships in the proposed study.

We include the $1 amount as it is possible that we ﬁnd ourselves in the blue, low-cost, scenario, in which the bulk of
the response rate increase can be generated with one dollar. However, the medium-cost scenario seems very plausible.
Mercer et al. (2015), for example found that, on average, in person surveys that paid $5 versus nothing had a response
rate increase of 5 percentage points, those that paid $10 versus nothing had an increase of 7 percentage points, while
those that paid $20 had an increase of 9 percentage points. In other words, while doubling the incentive from 5 to 10
produced a 40 percent increase in effectiveness, doubling it from $10 to $20 only produced a 28 percent increase in
effectiveness.
For this reason, we believe it makes sense to test an amount of $10. Moreover, the panel context of the AHS argues in
favor of including at least one substantial incentive amount. In particular, it is important to know how incentives in one
wave affect response patterns in subsequent waves. While respondents may very easily forget having received $1 or
$5 two years ago given the largely symbolic value of these sums, $10 seems more likely to stand out in one’s memory.
This raises the prospect that, either through habit-formation or recall, large incentive amounts may durably increase
response rates beyond the one wave in which they are conducted or lead to an expectation of similar incentives in
future waves. This is a possibility largely unexplored in the literature.

2.4 Remaining gaps in the literature
While the literature we review below shows that incentives are effective at increasing response rates, there are three
gaps, some of which the present study aims to ﬁll but others that remain for future research.
First, despite recognition that increasing the response rate overall does not necessarily reduce nonresponse bias
(Groves 2006), studies largely continue to focus on response rates as the outcome to improve rather than measures
of bias. In a meta-analysis published seven years after the points made by Groves (2006), Singer and Ye (2013) note
an ongoing lack of research into the ability of incentives to address nonresponse bias. Since then, both Crissey,
Christopher, and Socha (2015) and Jackson, McPhee, and Lavrakas (2020) target measures of bias as outcomes in
http://oes.gsa.gov

addition to response rates, benchmarking characteristics of respondents to known quantities, but their studies have
yielded no discernible improvements in bias from targeting.7 Our study continues their work in examining reductions
in bias, rather than improvements in response rates, as the primary outcome.
Second, Jackson, McPhee, and Lavrakas (2020) is the ﬁrst study of which we are aware to experimentally compare the
impact of: (1) incentives given independent of a household’s response propensity (respondents randomly assigned to
$2 or $5) to (2) incentives based on response propensities, with higher amounts given to those with lower propensities
and no incentive given to those with a high response propensity. However, because the second condition involved
giving escalating incentives based on propensities, it does not allow us (1) to compare the full range of incentives ($0$10) in all strata of response propensities or (2) to compare a strategy of randomly deciding who receives any incentive
to a strategy of giving incentives to those with high nonresponse propensities. The design we outline below aims to ﬁll
these gaps.
Finally, and returning to the three groups we outlined above—(1) those with low response propensities; (2) those with
low response propensities who have the highest likelihood of contributing to bias; (3) those with low response propensities, high bias-contribution likelihoods, and a high likelihood to be “moved” to respond by incentives—all existing
research either targets group one (Jackson, McPhee, and Lavrakas 2020) or a combination of groups one and two
(Crissey, Christopher, and Socha 2015; Coffey and Zotti 2015). As Jackson, McPhee, and Lavrakas (2020) note:
“An important outstanding question is whether it is possible to classify cases based not only on their base response
propensity but also on the increase in response propensity that would be attributable to (for example) a higher incentive. If cases are heterogeneous in their sensitivity to an intervention, and if this sensitivity can be predicted from
auxiliary data available prior to collection, then it may be efﬁcient to target the intervention based on predicted sensitivity” (407).
Because our study will randomly allocate amounts across propensities, it will take a step toward addressing this gap.
In particular, our study should permit the construction of “sensitivity scores” that will enable future incentive studies
to test this third type of targeting.

2.5 Intervention Design
The intervention involves providing incentives randomly in one randomly-selected half the sample and, in the other
randomly-selected half, providing incentives only to those predicted to not respond absent incentives. We deﬁne its
features with the aid of some simple formal notation.
Let there be a universe, U , of individuals indexed i, who comprise a ﬁxed and ﬁnite population of size N whose characteristics some decision-maker would like to learn. Speciﬁcally, suppose that individuals have a feature, Xi , whose
¯ = 1 ∑
true mean the decision-maker would like to learn: X
i∈U Xi . For example, this might represent the true
N
¯ , the decision-maker takes a random sample of n
rate of severely inadequate housing in the United States. To learn X
individuals. Let Si ∈ {0, 1} denote a random variable that indicates selection into the sample. Sample probabilities
are πiS = Pr(Si = 1). We let Yi ∈ {0, 1} denote an indicator for response, and R the set of individuals who are
both sampled and who respond, R = {i : Si = 1, Yi = 1}. The decision-maker can only observe the feature for
¯ , she uses the weighted sample mean estimate
those who are sampled and who respond. In order to learn about X

ˆ¯ = ∑
X
i∈R Xi wi , where wi is a sampling or bias-adjustment weight that sums to 1 (wi =

∑

1/πiS
S ).
i∈ R 1/πi

Suppose that the decision-maker has a ﬁxed monetary budget, B , that she can use to incentivize potential respondents
to respond to her survey. Denote by bi ∈ R+ , a positive dollar amount, the budget allocated to the i’th respondent.
Suppose further that:
7

More precisely, Crissey, Christopher, and Socha (2015) only ﬁnd improvements in bias when the promised incentive for completing the
survey is $45.

http://oes.gsa.gov

• the i’th potential respondent has an unobservable propensity to respond, ηi = Pr(Yi = 1),
• ηi is correlated with the covariate of interest, Xi , which is either ﬁxed and not changeable by attempts at contact (e.g., age) or measured prior to the attempt at contact (e.g., percentage of household income paid towards
rent)
• propensities are increasing (monotonically but possibly nonlinearly) in bi (∂ηi /∂bi > 0 ∀ i), and
• ηi ∈ (0, 1) ∀ i.

¯ = 1 ∑n
The response rate for a given sample is given by Y
{i:Si =1} Yi . Since Si is a random variable, we can deﬁne
n

¯ ]. We can also deﬁne the expected sample mean of Xi over
the expected response rate over random samples as E[Y
ˆ
¯.
random samples as E[X]

With this setup and sufﬁciently large samples (e.g., large enough n), the problem is that under a no-spending world
(bi = 0 ∀ i), it follows that:
• some potential respondents will respond and others will not, so that the expected response rate is not 100%
ˆ
¯ ] ̸= 1), which increases uncertainty by increasing the variance of the sample mean estimate (E[X
¯ 2] −
(E[Y

ˆ¯ 2 ),
E[X]

¯−
• respondents will have different covariate proﬁles than non-respondents, with nonresponse bias deﬁned as X
ˆ
¯ . In general, we expect covariates to differ between people who respond and those who do not (for examE[X]
ple, responders may be older, on average, than non-responders).
This situation represents the status quo, in which no incentives are used. In expectation, decisions made on the basis
ˆ¯ will be less certain as E[Y¯ ] decreases (lower expected response rate), and more biased as X
ˆ
¯ − E[X]
¯
of some X
increases in absolute size. The problem is thus to improve decision-making by devising some optimal way of allocating
incentives, b∗ (with 0 ≤ b∗i ≤ B ∀ i), so as to achieve two aims:

¯ ]; and,
1. Maximize the expected response rate, E[Y
ˆ
¯ − E[X]|
¯ .
2. Minimize nonresponse bias, |X
Informally, what might an optimal b∗ look like? Focusing ﬁrstly on the response rate, it seems obvious that spreading
the budget too thinly is unlikely to provoke any change in response: providing someone with ﬁve cents might not be
enough. So, unless B is very large or propensity to respond is highly responsive to even very small increases in incentive amounts, the strategy in which every respondent is given an equal share of B (i.e. bi = B/n) is dominated by one
in which a subset of size m < n of all potential respondents is provided a cash incentive. For example, if the expected
¯ ])n, so that the proportion of the sample that
response rate can be reliably calculated, one might set m = (1 − E[Y
receives incentives, m/n, is equal to the proportion expected to not respond.
As noted above, this raises the question of how much does the incentive needs to be concentrated in order to cause a
substantial increase in response: e.g., is one dollar enough or are ﬁve dollars necessary? Are there diminishing marginal
returns, such that, for example, providing one dollar versus no dollars increases response much more than providing
eleven versus ten dollars (i.e., ∂ 2 ηi /∂ 2 bi < 0)? Providing accurate answers to these questions ensures that neither
too much nor too little is spent on incentives in order to achieve the two aims.
It also raises the question, addressed only imperfectly in the literature described above, of how that subset should
be chosen. If it were possible to glean information on propensities to respond, would allocating incentives to those
with the lowest ηi increase response?8 In addition, if the targeting is to those with the lowest propensity to respond,
8
This does not strictly have to be the lowest ηi but can be those with relatively lower propensities, for example, those deemed close to the
margin of responding; however, the general logic of targeting is the same even if the selected set of propensities for targeting is somewhat

http://oes.gsa.gov

is there a subset of these low-propensity individuals who are most likely to introduce bias if not incentivized—that is,
individuals that have attributes of interest that differ from those with high response propensities? How large would
the gains from such an approach be?
In practice, decision-makers do not get to observe response propensities when deciding how to allocate incentives.
Moreover, incentives are often used in the context of experiments. Thus, more often than not, incentives are allocated
independently from any potential respondent characteristics.
In theory, however, one potentially more optimal b∗ would allocate none of the budget to those respondents who will
respond even in the absence of incentives, because it is inefﬁcient to offer incentives to those who would respond
without the additional inducement. Allocating the incentive budget to those most likely to contribute to nonresponse
bias would instead optimize the incentive budget in line with the goals listed above.
Suppose that the decision-maker has access to an estimated propensity, ηˆi , which includes both the propensity to respond and a likelihood of introducing bias. There is a spectrum of ways in which she could allocate incentives to m
respondents as a function of their estimated propensities. At one extreme of the spectrum, she might allocate incentives completely independently of propensities (Pr(bi | ηˆi ) = Pr(bi ) ). At the other end of the spectrum, she may
allocate incentives to respondents as a deterministic function of their estimated propensity. We compare the two
extremes of this spectrum of allocation mechanisms:
1. Propensity-Independent Allocation: incentives are allocated to potential respondents independently of their
true or estimated propensities Pr(bi | ηi ) = Pr(bi ).
2. Propensity-Determined Allocation: potential respondents are indexed in order of their estimated response
propensities, ηˆi , so that ηˆ1 = min(ˆ
ηi ) and ηˆn = max(ˆ
ηi ). The key feature of this assignment is that incentives
are deterministically provided to those respondents deemed most at risk of nonresponse (Pr(bi > 0 | i ≤
m) = 1) and no incentive is provided to the rest of the respondents (Pr(bi > 0 | i ≥ m) = 0). In addition,
this propensity-determined allocation may compare (1) different methods for estimating the propensity (e.g.,
comparing a simple rule based on previous nonresponse behavior to a more complex model) and (2) may target
modiﬁable forms of nonresponse (e.g., refusals in previous waves) rather than all forms of nonresponse.

3 Evaluation Design
We are interested in understanding how propensity-determined allocation of incentives affects nonresponse bias and
how the size of incentives delivered to a potential respondent affects the rate of response among different subgroups
in the sample. The randomization is designed to generate the counterfactuals necessary to make these quantities estimable. We deﬁne these counterfactuals below.
Continuing from the formalization above, the evaluation imagines that those sampled into the 2021 AHS survey could
have been allocated incentives using either of the two allocation mechanisms above. Let Zi ∈ {0, 1} denote a random
variable that indicates whether potential respondent i has been assigned to receive an incentive.
First, we denote by Z T =0 the allocation of incentives that would have obtained had Propensity-Independent Allocation been used for the entire sample. An n-length vector of m 1s and n − m 0s is generated, in which there is no
dependence of the assignment on estimated propensities: Pr(ZiT =0 = 1 | ηˆi ) = P r(ZiT =0 = 1) ≈ .3. The 1s and
0s are simply shufﬂed among the potential respondents.
Second, we denote by Z T =1 the allocation of incentives that would have obtained had Propensity-Determined Allocation been used for the entire sample. The potential respondents are sorted by their ηˆi , from lowest to highest, and
an n-length vector of m 1s and n − m 0s is generated (with the 1s at the top and the 0s at the bottom.) Thus, those m
shifted.

http://oes.gsa.gov

respondents with the lowest 30 percent of estimated propensities are guaranteed to receive an incentive, and those
n − m respondents with the highest 70 percent of estimated propensities are guaranteed not to receive an incentive. Note that this represents a considerable advantage: with an expected response rate of 74 percent, if our model
does well at predicting nonresponse, we would be targeting all predicted nonrespondents—including both those on
the margin and those who are perhaps less likely to be converted to responses—but a minimum of those already likely
to respond.
We deﬁne the vectors Z T =0 and Z T =1 for the full sample: these are the assignments that would obtain, were we to
use propensity-independent or -determined allocation methods for the full survey. These are the allocation counterfactuals.
From here, we suppose that every respondent has a potential outcome function, Yi (Zi ). In particular, we imagine that
Yi (ZiT =0 = 1) = Yi (ZiT =1 = 1) and Yi (ZiT =0 = 0) = Yi (ZiT =1 = 0), so that if the potential respondent
would have (not) responded when (not) assigned to an incentive under one allocation scheme, they also would have
(not) responded when (not) assigned to an incentive under the other. Some research has shown that knowing that
one is in a lottery-style incentive condition versus deterministic condition could matter for responses. However, since
respondents will not know that they are being randomly assigned to conditions here, we don’t have reason to doubt
this assumption.
This stability in the potential outcomes allows us to deﬁne, for a given Z T =0 and Z T =1 , the outcomes that would have
resulted had one or the other allocation schemes been used to assign incentives.
The experiment works by generating Ti ∈ {0, 1} (for “targeting”): when Ti = 0, the individual is given the Zi corresponding to Z T =0 and they reveal the Yi that corresponds to Yi (ZiT =0 ); when they are given Ti = 1, they are
given the value of Zi that corresponds to ZiT =1 , and reveal the outcome that corresponds to Yi (ZiT =1 ). The targeting variable, Ti , is generated by sorting individuals by an estimated propensity to respond, forming consecutive pairs,
and ﬂipping a virtual coin within each pair. We thereby obtain one “random sample” from the world in which we did
propensity-determined allocation and one from the world in which we did propensity-independent allocation. The
pairs ensure that, for any given tranche of propensities, there will be near-perfect balance with respect to T .
One concern with such a procedure is that it generates correlation between Zi and ηˆi and Xi . In other words, the assignment creates confounding between propensity to respond, probability of assignment to treatment, and the characteristics we care about.
As it turns out, however, this is a simple case of heterogeneous assignment probabilities. And, as we show below, it
is easily dealt with using an inverse propensity weighted estimator. Speciﬁcally, since T is independent, for any given
individual the probability of assignment is given by Pr(Zi = 1) = Pr(Ti = 1) × P r(Zi = 1 | Ti = 1) + Pr(Ti =
0) × P r(Zi = 1 | Ti = 0). For the 30% (m/n) of units with the lowest propensity to respond (who will be allocated
an incentive under targeting), this evaluates to .5×1+.5×.3 = .65. For the 70% of units with the highest propensity
to respond (who will not be allocated an incentive under targeting), this evaluates to .5×0+.5×.3 = .15. Thus, there
Z (where z indicates an observed treatment status):
are four possible values of a treatment assignment probability πi,z
Z = .65 and π Z = 1 − .65 = .35; for k high propensity individuals, π Z = .15
for j low propensity individuals, πj,1
j,0
k,1
Z = 1 − .15 = .85. Thus, it is possible to observe every unit in every treatment condition, albeit with
and πk,0
differing probabilities. To obtain unbiased estimates of the average treatment effect, we simply downweight those
Z , the
who are overrepresented in treatment or control, and upweight those who are underrepresented, using 1/πi,z
inverse treatment propensity.

ˆ¯ . This drastically
Note that there is no biasing path that confounds T and other outcomes of interest, such as Yi or X
simpliﬁes the estimation of unobservable quantities such as the proportion of respondents with Xi = 1 who would
ˆ¯ | T = 1].
respond to the survey, if a propensity-determined allocation method were used for the whole sample: E[X
i
In simulation studies, we are thus well-positioned to see both whether the deterministic allocation would produces an
http://oes.gsa.gov

actual increase in the representativeness of the sample, and also whether our estimators are able to recover this.
Finally, while the variation in T that generates variation in Z is the main variation we are interested in, we are also
interested in the elasticity of incentives to response: ∂ηi /∂bi and ∂ 2 ηi /∂ 2 bi . Thus, among those m assigned to incentives, we plan to vary the amount of the incentive between 1, 5, or 10 dollars. This enables us to study the change
in ηi induced by a one-unit change in bi . As we describe in greater detail below, this dose-response function could
be highly non-linear. However, we are able to recover an estimand that is deﬁned as a linear transformation of the
potential outcomes using a linear estimator, even though the potential outcomes are generated through a non-linear
process. See Figure 4 above for a graphical illustration of this point.

3.1 Total Number of Observations
The 2021 AHS integrated national sample will build on the existing panel created by sampling just over 85,000 units
in 2015. We anticipate that the ﬁnal sample will be close to 84,000.

3.2 Randomization / Assignment
There are three variables that are randomly assigned: Ti ∈ {0, 1} is an indicator for whether the unit receives
the allocation they would have received under the Propensity-Determined (versus Propensity-Independent) method;
Zi ∈ {0, 1} is an indicator for whether the individual is assigned to receive any incentive amount in the allocation
used; Ai ∈ {0, 1, 5, 10} is the dollar amount allocated to each potential respondent. The procedure for the random
assignment works as follows:
2. Create ZiT =1 . Order each potential respondent from highest to lowest ηˆi . Calculate m ≈ .3 × n, and assign
the ﬁrst m − n individuals to ZiT =1 = 0 and the last m to ZiT =1 = 1. This provides the vector Z T =1 : the
assignment that would have obtained, had each unit been assigned using Propensity-Determined Allocation.
3. Create ZiT =0 . Deﬁne f () as a function that randomly sorts a vector, and set ZiT =0 = f (ZiT =1 ). This provides
the vector Z T =0 : it is the assignment that would have obtained, had each unit been assigned to incentives using
Propensity-Independent Allocation.
4. Create Ti . Sort individuals in order of their estimated propensity (randomly resorting within equal propensities)
and form them into consecutive pairs. Within each pair, assign one individual to Ti = 1 and one to Ti = 0 with
.5 probability. If there is an odd number of individuals, randomize the last unit using a coin ﬂip.
5. Create Zi . For all units for whom Ti = 1, set Zi = ZiT =1 , and for those for whom Ti = 0, set Zi = ZiT =0 .
6. Create Ai . Among units where Zi = 1, randomly assign 50% to Ai = 10, 25% to Ai = 5, and 25% to Ai = 1.
Assign the remaining sample for whom Zi = 0 to Ai = 0.

3.3 Treatment Conditions
The random assignment of the three variables, A, Z , and T , results in eight treatment conditions. The large number
of conditions may sound like it puts the study at a risk of low power, but in practice the study is not analyzed as a multiarm design. Mostly, estimands are deﬁned by marginalizing over conditions to obtain a difference in two conditions.
The table below translates the procedure above into proportions and sample sizes, based on an approximate sample
size of 84,000.
Propensity-Independent (50%)
Incentive $ amount:
Incentive proportion:
Total number:
Sample proportion:

0
70%
29,400
35%

1
7.50%
3,150
3.75%

5
7.50%
3,150
3.75%

10
15%
6,300
7.50%

http://oes.gsa.gov

Propensity-Determined (50%)
0
70%
29,400
35%

1
7.50%
3,150
3.75%

5
7.50%
3,150
3.75%

10
15%
6,300
7.50%

3.4 Outcomes
At this stage, we are interested in three main outcomes, and three secondary outcomes. These will likely evolve somewhat as we begin to reﬁne the analysis plan.
Main Outcome: Effect of propensity-determined allocation on the difference in sample and population mean of key
outcome or covariate

• Interpretation: This outcome focuses on whether propensity-determined incentive allocation makes sample
estimates of outcomes such as home ownership less biased and, when concerning demographic variables,
whether it improves representativeness. We discuss measures of representativeness in the AHS nonresponse
bias memo Sections 2 and 5. The main outcome is the distance of the mean of Xi in the sample versus in
some reference population. For example, Xi may be a binary indicator for whether the householder owns
the housing unit outright, which is a key outcome for the AHS that is also measured in the Decennial Census.
Our separate analysis suggests this quantity is overestimated, even when using bias adjustment weights, so
ˆ
¯ − E[X]
¯ will be strictly positive. We expect that changing from random to deterministic allocation
that X
decreases this quantity.

ˆ¯ | T = t] the estimated mean of
¯ the true population mean of Xi , and E[X
• Deﬁnition of estimand: Denoting X

ˆ
¯ − E[X
¯|
Xi among those in the sample who respond when the allocation mechanism is t, our estimand is: (X
ˆ
¯ | T = 0]).
¯ − E[X
T = 1]) − (X

¯ − Xi on Ti . We refer to this estimand as “Effect of T on
• How we estimate it: Regress the distance of Di = X
sample vs pop. mean(X)” in design diagnosis below.
Main Outcome: Effect of propensity-determined allocation on response rate

• Interpretation: This is the average effect of propensity-determined allocation on the overall response rate. Per
the formalization above, we should expect propensity-determined allocation to increase the overall response
rate relative to propensity-independent allocation, as well as increasing representativeness.
1 ∑
• Deﬁnition of estimand: n
{i:Si =1} Yi (T = 1) − Yi (T = 0).

• How we estimate it: We regress Yi on Ti . In the design diagnosis below, we refer to this estimand as the “Effect
of T on Y”.
Main Outcome: Effect of a one-dollar change in incentive amount on response rate

• Interpretation: This outcome measures how much a one-dollar change in the amount of the incentive increases
average response rates, linearly. Our estimand is a parameter from a model applied to the potential outcomes:
it can be thought of as the coefﬁcient one would get on A if one were to able to ﬁt a least squares model to all
possible potential outcomes on all possible conditions for all units. Note: we are thinking of A as continuous
under this deﬁnition.
• Deﬁnition of estimand: the β that solves:
min
(α,β)

∑∫

(Yi (x) − α − βA)2 f (A)dA

• How we estimate it: We regress Yi on Ai in a weighted least squares model, in which the weights are the inverse of the probability of observing unit i in condition Ai = a. In other words, each unit’s contribution to the
likelihood is weighted by Pr(A1 =a) . In the design diagnosis below, we refer to this estimand as the “Change in Y
i
caused by unit change in A”.
http://oes.gsa.gov

Main Outcome: Effect of being sent an incentive on response rate

• Interpretation: This is the average effect of being sent any incentive on the response rate.
• Deﬁnition of estimand: Assuming homogeneous effects for incentive amounts for ease of exposition, it is simply
1 ∑
{i:Si =1} Yi (Z = 1) − Yi (Z = 0). Under heterogeneous effects, it is the average of the unit-level
n

1 ∑
1 ∑
averages of three estimands: n
{i:Si =1} Yi (A = 10)−Yi (A = 0), n
{i:Si =1} Yi (A = 5)−Yi (A = 0),
1 ∑
and n
{i:Si =1} Yi (A = 1) − Yi (A = 0).

• How we estimate it: We regress Yi on Zi in a weighted least squares model, in which the weights are the inverse of the probability of observing unit i in condition Zi = z . In other words, each unit’s contribution to the
likelihood is weighted by Pr(Z1 =z) . In the design diagnosis below, we refer to this estimand as the “Effect of A>0
i
on Y”.
Secondary Outcome: Effect of propensity-determined allocation on sample mean of covariate

• Interpretation: This is the average effect of propensity-determined allocation on the mean of some covariate.
This can be thought of as a more direct estimate of bias in the sense that we are able to directly observe estimates of key outcomes of interest for both treatment contitions. If propensity-determined allocation changes
the proportion of groups likely to introduce bias above a propensity-independent allocation, we should be able
to estimate this increase.

ˆ
ˆ¯ | T = 0].
¯ | Ti = 1] − E[X
• Deﬁnition of estimand: E[X
i
• How we estimate it: We regress Xi on Ti . In the design diagnosis below, we refer to this estimand as the “Effect
of T on sample mean(X)”.
Secondary Outcome: Effect of incentives on number of contact attempts

• Interpretation: This is the average effect of being sent any incentive on the number of contacts attempted with
a respondent (successful and unsuccessful interviews).
1 ∑
• Deﬁnition of estimand: n
{i:Si =1} Yi (Z = 1) − Yi (Z = 0).

• How we estimate it: We regress Yi on Zi in a weighted least squares model, in which the weights are the inverse
of the probability of observing unit i in condition Zi = z .

3.5 Meaningful Effect Size
In our simulation studies of this design, we deﬁne potential outcomes in the following way:

Yi (Zi = 0) = Binom(ηi )
{
1
Yi (Zi = 1) =
Binom(τ )

(1)
if Yi (Zi = 0) = 1
if Yi (Zi = 0) = 0.

(2)

Where τ is the effect of the incentive on if-untreated non-responders (those for whom Yi (Zi = 0) = 0). Providing incentives is assumed here to only affect those who would not have responded when no incentive was provided,
and only increases the likelihood of response: we rule out cases where providing an incentive causes nonresponse in
someone who would have responded in the absence of incentives (although, in theory, such cases are possible – say, if
control responders are so offended by receiving a dollar they decide not to respond).

http://oes.gsa.gov

Thus, we can distinguish between τ , the average effect of receiving an incentive among if-untreated non-responders,
and τ , the average effect of receiving an incentive in the sample.
We think that anything above a 1 percentage point increase in the overall response rate is a meaningful effect. Note
that τ = (1 − Y ¯
(0))τ . In the 2017 AHS, for which we can only observe units in the control condition, we have
¯
Y (0) ≈ .80. So, we can back out the (constant) effect incentives would have to generate among if-untreated nonresponders in order to obtain τ = .01 using .01 = (1 − .80)τ , which implies τ = .01/.20 = .05. Thus, in
order to observe a sample average treatment effect of a one-percentage point increase in the response rate (τˆ = .01),
incentives would need to increase the response probability of if-untreated non-responders by ﬁve percentage points
on average. This seems like a reasonable bar to clear.

3.6 Likely Effect Size
Singer et al. (1999) compared the results of 39 experiments on ﬁnancial incentives in face-to-face and telephone
surveys. The effect sizes were smaller (though not statistically signiﬁcantly so) for face-to-face surveys, translating
to a one-third percentage point increase in response rates for each dollar spent. The treatment group will receive
1 × .25 + 5 × .25 + 10 × .5 = 6.5 USD on average, implying a likely average effect of .003 × 6.5 = .02 = τ . In
terms of average effects on if-untreated non-responders, this implies a 10 percentage point increase (τ = .10). These
parameters are assumed in the power calculations below.

3.7 Power
Using DeclareDesign, we conducted a preliminary diagnosis of the design’s ability to estimate the outcomes described above, assuming τ = .10 and τ = .02. In addition to power, we are able to diagnose the bias, coverage, and
variance properties of the different estimator-estimand pairs.
Estimand Description

Mean
Estimate

Mean
Estimand

Bias

Power

Coverage SD Estimate

Mean
SE

Effect of T on sample vs pop. mean(X)
Change in Y caused by unit change in A
Effect of A>0 on Y
Effect of T on Y
Effect of T on sample mean(X)

-1.20
0.70
2.00
0.98
1.20

-1.20
0.70
1.93
1.00
1.20

0.00
0.00
0.07
-0.01
-0.00

1.00
1.00
1.00
0.95
1.00

0.97
0.96
0.95
0.96
0.97

0.11
0.04
0.31
0.27
0.11

0.10
0.04
0.29
0.27
0.10

The numbers are scaled to reﬂect percentage point changes. The ﬁrst row can thus be interpreted as follows: the average estimate of the “Effect of propensity-determined allocation on the difference in sample and population mean
of covariate” is -1.20 percentage points, and so is the average value of the estimand. Thus, the bias for this estimator
is zero. The power is 1, implying the design is able to reject the null given the true underlying -1.20 percentage point
reduction. The 95% conﬁdence interval covers the true estimand 97% of the time. This is most likely indicative of
simulation error, and possibly some slight conservative bias in the standard errors, which is to be expected. The standard deviation of estimates across the sampling distribution generated by the simulations – the “true” standard error
– is one-tenth of a percentage point, which is approximately equal to the average standard error estimated (again, the
standard errors appear very slightly conservative). Overall, the average estimate is ten times greater than the average standard error, indicating a high degree of statistical power. The conclusion is that the design does a very good
job of estimating an increase in representativeness using this particular deﬁnition of representativeness (decrease in
underrepresentation of X = 1).
Moving to the rest of the table, the estimators and estimands are all signed as we would expect. Proceeding
row-by-row: the propensity-determined allocation method produces less distance in estimates of x compared

http://oes.gsa.gov

to the propensity-independent method; each extra dollar has a linear effect on the response rate equal to .70
percentage points; receipt of any incentive increases the response rate by two percentage points on average;
propensity-determined allocation increases the response rate by one percentage point more on average than
propensity-independent allocation does; and propensity-determined allocation also increases the proportion of
respondents with Xi = 1 (the simulations assume such respondents are ordinarily underrepresented).
In general, the estimators are all well-powered given the large sample size and the assumptions of the simulation. Comparing point estimates to standard errors, the change in Y caused by unit change in A estimator is clearly the most efﬁcient: the point estimate is over seventeen times larger than the standard error on average. This estimator is thus our
best-powered.
There is a very small amount of bias in two of the estimators. This is likely due to simulation error, either in the simulations for the diagnosis, or in the simulations used to generate assignment weights. It is small enough, at less than
one-tenth of a percentage point, as to be negligible. As mentioned, there is little concern for false positives from the
standard errors: if anything, they exhibit a small amount of the well-documented Neyman standard error bias that
results from underestimation of the covariance in potential outcomes.

3.8 Data
We currently have access to the 2015, 2017, and 2019 AHS Integrated National Samples. We also have datasets we
will use to estimate propensities, namely: the 2018 public-access Census Planning Database, as well as the (1) AHS
2015, 2017, and 2019 “CHI” datasets, which provide metadata on nonresponse for all units, and (2) trace ﬁles for all
three waves that provide more detail on each unit’s progression through the survey instrument. This data is sufﬁcient
to conduct randomization and hand off to partners at the Census Bureau.

3.9 Anticipated Limitations
There are a handful of risks worth highlighting. For the ﬁrst three, we have conducted analyses that we outline in the
accompanying summary memo–“Nonresponse Bias in the American Housing Survey 2015-2019”–that address the
ﬁrst three limitations.
1. Our propensity model may not be good. The design assumes that we are able to estimate ηi in a reasonably informative way. If we don’t have good propensity estimates, then any allocation of incentives on the basis of such
estimates will be weaker. However, we are in a very favorable context in this study: we have panel data that has
two years’ worth of information about how respondents behaved in the past, as well as tract-level demographic
information from the American Community Survey.
• How we address: In section 3 of the summary memo, we show that we can predict both nonresponse and refusal with a very high degree of accuracy in the 2017 and 2019 AHS. The most important predictors are past
behavior—e.g., if a unit was a refuser in 2017 they are signiﬁcantly more likely to continue to refuse in 2019.
However, area-level demographics were also important predictors. We will use these ﬁndings to improve our
ability to estimate ηi in the targeting experiment.
2. Developing estimates of X from AHS data will be complicated. The AHS data is not a simple random sample
– data needs to be re-weighted to account for the sampling procedure in order to generate estimates. And our
data also needs to be weighted by the inverse of the assignment propensities. So there is some complication
here that is something of a risk – we need to make sure we get the weights right in order to say something
meaningful about representativeness.
• How we address: in the summary memo, we discuss two considerations when comparing the AHS to benchmark
data (in that case, the Decennial census). First is making sure that we align the variable deﬁnitions in each of the

http://oes.gsa.gov

samples, which includes ensuring that we compare households to other households and that we compare questions asked in similar ways. Second is reweighting to account for the complex survey design. In the memo, and
in follow-up discussions on proper weighting methods, we believe we can generate estimates of X to properly
compare to a benchmark population, both at the national and the CBSA level.
3. Response bias may not be strong enough to detect a reduction. If the magnitude of nonresponse bias is small,
any correction of them will be very small, and thus hard to detect. There is not a great deal we can do about
this risk – we have designed as well-powered a study as we can. We could possibly think about how to include
covariates or focus the estimation on areas where underrepresentation is particularly strong.
• How we address: the memo indicates substantial divergence between the AHS and the benchmark for certain
characteristics. We believe this divergence is large enough to leave room for reductions in this distance.
4. Spillovers due to stopping rule. The Census Bureau typically stops data collection once the target of an 80%
response rate has been met. This poses a spillover concern for us: if we increase the response rate in area 1,
then we may also decrease it in area 2 by reducing the need to collect more data there in order to achieve an
80% response rate.
• How we address: The spillover issue is of particular concern for allocation methods that target at the area level.
To address this, we have located our randomization at the respondent-level, where shifts in allocation of effort,
which are coordinated by ﬁeld ofﬁcers, are unlikely. To assess robustness to spillovers, we will specify in the
analysis plan a stop date, before which we believe spillovers of this kind will have kicked in, and at which we will
estimate effects.

http://oes.gsa.gov

4 Appendix

http://oes.gsa.gov

AHS-33B(L)
(04-08-2019)

UNITED STATES DEPARTMENT OF COMMERCE
Economics and Statistics Administration

U.S. Census Bureau
Washington, DC 20233-0001

Thank you in advance for your participation in this survey.

Dear Community Member,
You recently received a letter from us about your participation in the American Housing Survey
(AHS). Soon, a Census field representative will contact you to participate in the survey.
What you need to know about the AHS:
• You are representing your community. You are one of a select number of
households chosen to represent thousands of others.
• The results are important. Policymakers, community leaders, nonprofit organizations,
businesses, and others use the results of the AHS for planning and programming in
communities across the United States--including yours. For example, the AHS helps
improve housing programs for the elderly and for first-time home buyers.
• Answering the survey is easy, safe, and secure. We will work with your schedule to
make answering the survey as easy as possible. The Census field representative will
show you their badge when they arrive to confirm their identity as a Census
employee, and all responses are confidential.
If you have other questions or want to learn more about the survey, please go to
. Thank you in
advance for your help with this important survey.
With gratitude,
The U.S. Census Bureau

Voltear para Español.

census.gov

AHS-33B(L)
(04-08-2019)

UNITED STATES DEPARTMENT OF COMMERCE
Economics and Statistics Administration

U.S. Census Bureau
Washington, DC 20233-0001

Le agradecemos de antemano su participación en esta encuesta.

Querido miembro de la comunidad,
Recientemente recibió una carta de nosotros sobre su participación en la Encuesta de
vivienda estadounidense (AHS). Pronto, un representante de campo del Censo se
comunicará con usted para que participe en la encuesta. Lo que debe saber sobre la AHS:
• Usted está representando a su comunidad. Usted es uno de un número selecto de
hogares seleccionados para representar a miles más.
• Los resultados son importantes. Los elaboradores de políticas, líderes comunitarios,
organizaciones sin fines de lucro, empresas, y otros tantos utilizan los resultados de la
AHS para la planificación y organización en comunidades a todo lo largo de los
Estados Unidos-incluyendo la suya. Por ejemplo, la AHS ayuda a mejorar los
programas de vivienda para la población de la tercera edad y para quienes compran
una casa por primera vez.
• Responder la encuesta es sencillo, seguro, y confidencial. Trabajaremos dentro de
su agenda, de manera que responder la encuesta le sea lo más fácil posible. El
representante de campo del Censo, le mostrará su credencial cuando llegue para
confirmar su identidad como empleado del Censo y todas las respuestas son
confidenciales.
Si tiene otras dudas o quiere saber más sobre la encuesta, por favor visite
. Gracias de
antemano por ayudarnos con esta importante encuesta.
Agradecidamente,
Oficina del Censo de los Estados Unidos

census.gov

AHS-33A(L)
(04-08-2019)

UNITED STATES DEPARTMENT OF COMMERCE
Economics and Statistics Administration

U.S. Census Bureau
Washington, DC 20233-0001

Thank you in advance for your participation in this survey.
Please accept this token of our appreciation.

Voltear para Español.

census.gov

AHS-33A(L)
(04-08-2019)

UNITED STATES DEPARTMENT OF COMMERCE
Economics and Statistics Administration

U.S. Census Bureau
Washington, DC 20233-0001

Le agradecemos de antemano su participación en esta encuesta.
Por favor, acepte esta muestra de nuestro agradecimiento.

census.gov

References
Ariely, Dan, Anat Bracha, and Stephan Meier. 2009. “Doing Good or Doing Well? Image Motivation and Monetary
Incentives in Behaving Prosocially.” American Economic Review 99 (1): 544–55. https://doi.org/10.1257/aer.99.1.544.
Armstrong, J. S. 1975. “Monetary Incentives in Mail Surveys.” Public Opinion Quarterly 39 (1): 111–16.
Coffey, S, and A Zotti. 2015. “Implementing Static Adaptive Design in the National Survey of College Graduates Using
the Results of an Incentive Timing Experiment.” In Joint Statistical Meetings.
Crissey, Sarah, Elise Christopher, and Ted Socha. 2015. “Adaptive Design Strategies for Addressing Nonresponse Error
in NCES Longitudinal Surveys,” 28.
Edwards, Phil, Ian Roberts, Mike Clarke, Carolyn DiGuiseppi, Sarah Pratap, Reinhard Wentz, and Irene Kwan. 2002.
“Increasing Response Rates to Postal Questionnaires: Systematic Review.” BMJ 324 (7347): 1183. https://doi.org/10.
1136/bmj.324.7347.1183.
Groves, Robert M. 2006. “Nonresponse Rates and Nonresponse Bias in Household Surveys.” Public Opinion Quarterly
70 (5): 646–75. https://doi.org/10.1093/poq/nfl033.
Groves, Robert M., Eleanor Singer, and Amy Corning. 2000. “Leverage-Saliency Theory of Survey Participation: Description and an Illustration.” The Public Opinion Quarterly 64 (3): 299–308. https://www.jstor.org/stable/3078721.
Hidi, Suzanne, and K. Ann Renninger. 2006. “The Four-Phase Model of Interest Development.” Educational Psychologist
41 (2): 111–27. https://doi.org/10.1207/s15326985ep4102_4.
Jackson, Michael T., Cameron B. McPhee, and Paul J. Lavrakas. 2020. “Using Response Propensity Modeling to Allocate Noncontingent Incentives in an Address-Based Sample: Evidence from a National Experiment.” Journal of Survey
Statistics and Methodology 8 (2): 385–411. https://doi.org/10.1093/jssam/smz007.
Laurie, Heather, and Peter Lynn. 2008. “The Use of Respondent Incentives on Longitudinal Surveys.” 2008-42. Institute for Social; Economic Research. https://ideas.repec.org/p/ese/iserwp/2008-42.html.
Link, Michael W., and Anh Thu Burks. 2013. “Leveraging Auxiliary Data, Differential Incentives, and Survey Mode to
Target Hard-to-Reach Groups in an Address-Based Sample Design.” Public Opinion Quarterly 77 (3): 696–713. https:
//doi.org/10.1093/poq/nft018.
Mercer, Andrew, Andrew Caporaso, David Cantor, and Reanne Townsend. 2015. “How Much Gets You How Much?
Monetary Incentives and Response Rates in Household Surveys.” Public Opinion Quarterly 79 (1): 105–29. https://doi.
org/10.1093/poq/nfu059.
Singer, Eleanor, John Van Hoewyk, Nancy Gebler, Trivellore Raghunathan, and Katherine McGonagle. 1999. “The
Effect of Incentives on Response Rates in Interviewer-Mediated Surveys,” 14.
Singer, Eleanor, and Cong Ye. 2013. “The Use and Effects of Incentives in Surveys.” The ANNALS of the American
Academy of Political and Social Science 645 (1): 112–41. https://doi.org/10.1177/0002716212458082.

http://oes.gsa.gov

File Type	application/pdf
File Modified	0000-00-00
File Created	2020-10-16