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LIBRARY

OF THE

MASSACHUSETTS INSTITUTE
OF TECHNOLOGY



in)28

.M414
67



WORKING PAPER
ALFRED P. SLOAN SCHOOL OF MANAGEMENT



CAUCAL INFERENCE

FROM CROSS-LAGGED CORRELATION COEFFICIENTS:

FACT OR FANCY?

Peer Soclberg '^LG ~(s'y




CAUCAL INFERENCE

FROM CROSS-LAGGED CORRELATION COEFFICIENTS;

FACT OR FANCY?



Peer Soclberg ' /2.L6 ^(a




260-67



(c^ Copyrisht by Peer Soelberg



The paper should not be reproduced in whole or in part,
by any process, without the author's permission.






PFCEIVED
J UN 'X^ 1967



CAUSAL INFERENCE FROM CROSS -LAGGED CORRELATION COEFFICIENTS:

FACT OR FANCY?

Introduction

Several writers, some of them independently of each other, have sug-
gested that the troublesome problem of inferring causal connections among
variables from non-experimental survey data can be solved by interpreting
patterns of so-called "cross-lagged" correlations among the variables, if
the latter are observed at two or more points in time, (Campbell, 1963|
Blalock, 196A; Pelz and Andrews, 1964; Farris, 1966; Yee and Gage, 1966;
Rozelle and Campbell, 1966). Readers not familiar with the cross-lag meth-
od are referred to a description of it on p. 10, below. None of the authors
mentioned have, however, offered particularly convincing arguments why
their cross-lagged method of inference should work. Appeal has simply been
made to an inituitive "obviousness" of the assertion that any variable
which causes another should be highly correlated with the second variable
measured at some appropriately delayed point in time. According to which,
by the logical fallacy of accepting the antecedent, the authors conclude
that any two variables which are found to be correlated over time according
to the specified pattern are ipso facto causally connected.



This paper is as a warning to those researchers who are tempted to use
the cross-lagged method for causal inference without more adequately under-
standing its underlying assumptions and limitations. We shall undertake to
show that, under some rather simple conditions, it is possible to "prove"
just about anything with the cross=lagged method of inference.

The paper thus constitutes the point of departure for the author's pro-
posed investigation of the analytical limitations of cross~lagged correlation
analysis. But before we describe the new method it will be useful, as back-
ground for our discussion, briefly to consider the three methods that tradi-
tionally have been used for imputing causality to relationships among vari-
ables, on the basis of discrete observations of the variables' behavior.

Traditional methods of causal inference

EXPERIMENTAL MANIPULATION: The effect of one variable upon another may
be inferred from the observation of non-chance differences in operational
measures of the latter "dependent" variable, under different experimentally
manipulated conditions (like "presence" versus "absence") of the former,
"independent" variable - provided that the effects of all other variables,
including the mere passage of time, have either been "controlled" for (i.e.,
randomized or held constant) during the experiment, or can be assumed a priori
to have no effect on the relationship among the variables under study.

The following table illustrates the different outcomes of an experiment
that would lead observers to infer that necessary versus sufficient causal
links existed between two variables, say A (here taken to be a dichotomous
"independent", or manipulated, variable) and JB (a "dependent", i.e. observed,
variable which is also assumed to be dichotomous);



-3-











B
o


Not-B
o








If A
o

and all other variables
that could possibly affect B
have either been randomized
or held constant


"ll


"12


If not -A
o

and all other variables

that could possible affect B

have either been randomized

or held constant


«21


^22









11 .



If N. ^ ~ ^1? (there is no "statistical difference" in the observed
number of cases, N, in each row cell, i.e., the hypothesis that the
observed difference could have arisen by chance cannot be rejected
with a reasonable degree of confidence) and if N^, = N-2 » then we
conclude that A, together with all the other variables held cons-
tant during the experiment, have no (resultant) effect on B.

If N^^ ^ ^19 ^^'^ ^91 ~ ^99' then we conclude that A , perhaps in combin-
ation with any or all of the other variables held constant during
the experiment, is a sufficient but not necessary condition for B
or not-B , as the case may be, depending on whether N. ^ -^ ^19 °^

^11 < Nl2>



iii . ^^^11 ~ ^12 '^^'^ ^o-i ^ ^99' "* conclude that A is a necessary but

not sufficient condition for B (or not-B )

o o



iv. If N. , 3^ N^„ and N-. f N_- , we conclude that, for the particular

values of the variables held constant during the experiment, A

is a necessary and sufficient condition for B (i.e. A and
■' o o

only A causes B - stochastically if N, „ and N_, are signifi-
■^ o o Iz id!

cantly different fron zero).
Should the experimental variables not be dichotomous , one would merely
add to the above matrix as many rows or columns as would be necessary to
differentiate the n or m different values of A or B, respectively - taking
care always to include the catch-all control category not-A. (i = 1, 2, . . , or
n-1) to test the causal necessity hypothesis.

Notice that experimental manipulation of A will yield no information
about whether or not B also causes A. In other words, if B in fact did cause
A in "the real world", an experimental intervention using A as its independ-
ent variable would provide not the slightest clue about such a feedback effect
of B on A. Thus generalizing from the results of a one-way experiment to the
world at large is precarious business if feedback among the variables studied
is likely to occur.

li/hy not therefore, one could argue, simply run two experiments for each
pair of variables studied, each experiment set checking on each suspected
causal direction? Unfortunately, the cumulative effect of non-linear feed-
back among two or more variables will generally be different from any simple
algebraic "sum" of the experimentally, separately determined one-way effects
of one variable upon the other. "Causation" between A and B, say, in a non-
linear feedback loop is likely to vary, seeming tc go at times in one direction,
then in another, depending on the particular dynamic state of the A-B system
at any specific point in time. This phenomenom will be demonstrated below,
(p. 13).



■5-



The chief characteristic to be noted from our brief overview of the
experimental method of causal inference is that it requires one to make the
a priori assumption that the causal link he is about to study experimentally
is in fact uni-directional . Feedback among the variables, such as is commonly
found in dynamic systems, simply needs to be assumed away before valid causal
inferences can be made from observed differences in the "effects" of "inde-
pendent" variables on "dependent" ones.

Let us in closing consider the merits of an often heard critisms
that traditional experimental methods are "static", i.e. cannot be used for
unravelling dynamic, i.e. t ime -dependent , relationships among variables -
always given the assumption that these djmamic relationships are in fact unidirect-
ional. This, however, is a spurious criticism of experimental method.
There's nothing preventing an experimenter from adding time -sub scripts to
his "dependent" observations (in our example, above, we might have tried
relating A to B j-.o)- Yet traditionally it appears that most experimenters
have simply assumed that the effect of A on B, if there was one, would have
worked itself out sufficiently quickly to have stabilized, or become sig-
nificant, in the time delay needed to perform the experimental measurements.

MODEL CONSEQUENCE REJECTION; In cases where direct experimental manipu-
lation is impossible, or for some reason prohibitive, resort is often taken
to the experimental manipulation of symbolic models of the real situation.
Thus, given a symbolic model of the presumed relationships among two or more
variables, mathematical analysis may yield one or more non-obvious, potenti^
ally surprising, consequences of the postulated model. If empirical observ-
ations of the relevant variables then turn out to be "sufficiently similar"



-6-



in pattern to the predicted relationship, the analyst will not reject his
model, i.e. will keep on believing in the casual connections between the
variables that he has described therein. If, however, empirical observation
does permit him to reject his derived hypothesis — and included with the
latter the primitive assumptions and operational definitions that building
the model had forced him to make - the analyst must now revise his model
in order better to fit the data , At this point he must go through the pre-
dictive consequence-testing cycle all over again, until at some point he has
satisfied himself, and his critics, that he has checked out his model in all
its many possible (in practice only the more sensitive) state variations.

We shall not bore the reader with lengthy illustrations of causal in-
ference through model building. Simon in Models of Man provides easy-to-
follow demonstrations of specific applications of the method. Yet it may be
useful to note in passing that a simple way of obtaining "potentially sur-
prising consequences" from a model is to employ two different models ■ — both
of which should appear a priori to be just as reasonable to persons familiar
with the subject matter under study — which just happen to yield contradic-
tory predictions about the behavior of certain variables under some observable
set of circumstances. Then, whatever the outcome of observations, one it
bound to obtain a surprising, i.e. "significant", result,

STATISTICAL EXPERIMENTATION: If it appears a priori reasonable to view
the interactions among a small set of variables (say three of them) as consti-
tuting a closed system, i.e., as being largely independent of variations in
any other ("exogneous") variable over the period of observation, then, if all
(three) variables are significantly correlated, it is in some circumstances



possible, through post hoc partical correlation analysis, by making some addi-
tional a priori assumptions about the time precedence among subsets (pairs)
of the variables, to rule out some of the possible causal explanations that
would be compatible with the observed pattern of co-variation, and perhaps
thus, by elimination of all but one, establish the causal relationship that
must exist in the system, (Simon, 1957).

Illustration of this method of post hoc statistical experimentation will be
useful fiar our later discussion. Consider the variable system x, y, Z: which, as
noted, we may view as a closed causal system by assuming that the error terms
in the variables are uncorrelated - an assumption we could check empir-
ically if we were willing a priori to specify the causal shape of the system.
Existence of correlated error terms in two or more variables would indicate
the presence in the system of one or more unrecognized variables, which thus
were exacting a systematic effect on the hitherto included variables. Such
unrecognized variables would then have to be identified (not always easy)
and included in the "closed" system — thereby usually expanding by orders
of magnitude the number of possible causal hypotheses in the system - in
order to make our causal inferences from partial correlation analysis valid.

Given the above closed system assumption, the following diagram generates
the 27 different causal explanations - ways in v?hich each variable could be
linked to the other all compatible with an observation of three significantly
non-zero first-order correlations among three variables:



©



® .-_^ ©





In order to establish a unique causal explanation by means of partial
correlation analysis, it turns out, like for the case of experimental manip-
ulation, that the existance of feedback loops among the variables must be
ruled Out a priori by making a suitable set of assumptions. Say for illus-
tration we assume that X and Z both precede Y in time, such that, since time
is uni -directional, Y cannot possibly "cause" either X or Z. Similarly we
may be able to state that Z always precedes X. The remaining causal connec-
tions in our completely intercorrelated three-variable system would then re-
duce dramatically to:




©



©



First-order partial analysis may now be able to establish which of the
three remaining causal link patterns, implicit in our last graph of the sys-
tem, could possible have produced the three observed zero-order correlations.
The definition of the first-order partial correlation of X versus Y, "con-
trolling for" Z, can be written:

'XY.Z = ('^XY " ^XZ-^YZ>/^1 - Hz^""^^ - '^YZ^>''

Thus one observes that whenever the first-order correlation coefficient be-
tween two variables, controlling for the effect of a third variable on both
of them, goes to zero, then this result may be taken to indicate that the
observed zero-order correlation had been spurious, i.e. had been caused by
the simultaneous operation on the two faced variables of the third, now
"controlled" variable.



Hence, to illustrate, given the remaining three causal explanations of
complete intercorrelatedness that are embodied by our last graph, we
obtain the following three decision rules:

Case 1 i^Yv.'/ ~ ^ implies:




Case 2 r



XY'Z 5^ but r^ = implies;




> Y



Case 3 r



XY'Z 3* and r ^ implies



ZY'X




> Y



Any other combination of causal links and first-order partial correlations
would be incompatible with i^. the initial observation of significant zero-
order correlations among all three pairs of X, Y, and Z; or ii_.
our a priori assumptions about the causal time-precedence, j ,e . absence of
feedback, between each variable pair.



•10-



Hcwever, we ought also to note at this point that the use of correlation
coefficients of any sort forces one to assume that the underlying relation-
s'liip between the correlated variables is linear (or else that the variables
have been suitably transformed to correct for non-linearity), and that the
tine period betx^een the correlated observations in each of the variables
(usually taken to be instantaneous, such that all matched observations are
made simultaneously) reflects the "true" time period in which the influence
of one variable on the other vi/ill largely have been affected. Violation of
either of the latter sets of assumption would further invalidate causal in-
ference by statistical experimentation throuf^h partial correlation analysis.

Cross-la.^ped correlation an al ysis

The cross-lagged correlation technique presumably tests for time prece-
dence among variables (which, as we saw, had to be assumed a_ priori for
partial correlation analysis to work) while simultaneously measuring their
strengths of association. For the single two-by-two case the cross-lagged
method of causal inference can be described as follows (paraphrased from
Pelz and Andrews, 1964):

Assume the existence of a system of two variables A and B - i .e . no
other variables impinge on A and B. In other words, as stated above, the
error terms of A and B, given the hypothesis about their causal connection,
are assumed to be uncorrelated . Measure the variables at two points in time:
A^ , A„ , and B. , B- . One can then obtain the following set of correlation co-
efficients, (note that the dotted lines in the figure below no longer repre-
sent causal links among the variables):



•11-














The proposed method of cross-lagged correlation analysis now asserts:
If A and B are causally related then the simultaneous zero-order correlation
coefficients, r^ and r_ , "will both be positive and about the same magnitude"
(Pelz and Andrews, p. 837). But this assertion is false, as will be demon-
strated below.

Moreover, "the horizontal (or lagged) correlations .... will reflect
the consistency in each variable over time" (Pelz and Andrews, ibid .) In
time-series analysis the horizontal coefficients a_ and b^ are usually labeled
"auto-correlation", which to be sure does reflect a "consistency" of sorts
among the variables. But auto-correlation is not such a desirable property
for analysts to have as Pelz and Andrews seem to imply. Usually auto=correl-
ation in time-series indicates trouble for most statistical techniques s which,
like correlation coefficients, which depend for their validity on independently
drawn samples of observations. Pelz and Andrews, hovjcver , indicate
no need for adjustment of one's conclusions from cross-lagged analysis due to
the existence of autocorrelation in the data.



•12-



The heart of the proposed method of causal inference from patterns of
cross-lagged correlation coefficients is found in the following interpret-
ation given by the authors to the remaining two of the six correlation co-
efficients displayed in Figure 1, namely a and p. (The decision rule below
is paraphrased from Farris, 0£. cit . p. 142):

Case la ; If a f* and p = 0, then A causes B.

Case lb ; If a = and P ?^ 0, then B causes A.

Case 2a ; If a ji' 0, p ?* 0, and a > p, then A causes B more than B causes A.

Case 2b ; If cx ^ 0, B ?* 0, and a < p, then B causes A more than A causes B,

Case 2c : If a f' 0, p ^ 0, and a = p, then A causes B as much as B causes A.

Farris does not mention the sixth possibility, namely, that both a =0
and p =0. Perhaps this case were not thought possibles given the observa-
tion of a significant r^ . (We shall demonstrate below that indeed it is
possible.) However, simple extrapolation of the above "logic" of cross-
lagged analysis suggests that our inference for this sixth case should be:

Case 3 : If a = 0, and p = 0, then A and B are causally unconnected.

This, perhaps severly paraphrased, is as much analysis as the authors
offer to support their contention that cross-lagged correlation patterns will
be valid indicators of the underlying causal connections among variables that
are observed at two or more points in time.

A simulation experiment

To set the stage for our proposed investigation of conditions that
define valid uses of the cross-lagged method of inference, we carried
out the following simple experiment:



■13-



Consider an artificial computer system consisting of only two variables i
A and B (we call them X and Y) . To make things just a little bit interest-
ing we prescribea the follovjing simple-minded relationship among X and Y:

where k^ and k„ are constants, and e. and e„ are uniform random deviates
with mean zero and fixed ranges. In other words, our little simu-
lated world will exhibit simple harmonic nine-period periodicity. To keep
things clean we applied cross-lagged analysis to data generated by only
one such harmonic period. Let us label our terms:

X: average index of satisfaction, running from 0.00 to 2.00 (Lo, Medium,
Hi), of individual research scientists working in electronic widget
companies .

Y: profits generated (in $-thousands) by the new widget products in-
vented and patented by the firm's research labseach year. (This
is our measure of scientific productivity.)

Period analyzed ; 1956 to 1965 inclusive (i.e. X, to X. and Y. to Y_) .

Samnle size : 30 widget companies that each employ (by convenient govern-
ment regulation) exactly 5 research scientists (whose individual
satisfaction scores v;ere averaged each year) .

All we now need is a set of initir.l values for the X's (or the Y's), in
order to start our simulated world off and running. We chose to generate
a time-series by the following set of equations:

X = e
1.2,3,7

^4,6,8 = ^^(^"^>^i

S,9 = ^"^i
The random numbers e were dra\m from a Rani Table of Uniformly Distributed

Deviates in the Sloan School Com^iutcr Facility.



-14-



Our sample data average satisfaction (X) and productivity measurers (Y)
for the thirth electronic widget manufacturers over a nine year period, "1956
to 1964, are presented below.



1956



XI



1957



X2



1958



X3



1959



X^



1960



X5



1961



X6



1962



X7



1963



X8



1964



X9



.8030


.4797


.7344


.8817


.8783


1.1635


.5870


1.0693


1.3280


.4410


.0624


.3 104


.5178


.2848


.5900


.5430


.5321


.6707


.1250


.6591


.5984


.4625


.1112


.8214


.4010


.5593


.1819


.6360


.0832


1.4912


.6121


.5639


1.9210


.8440


1.2976


1.0162


.6110


1.2597


.0704


1.1355


.5263


.5185


.7450


.5932


.8881


.1540


.9672


.8416


.7637


.2178


1.3148


.5350


1.0403


.3929


.9450


.7436


1.3712


.9734


.9186


1.9341


.8750


1.6035


1.3808


.4240


1.0543


.9936


.871Q


.^800


1.4057


.2110


1.1069


.7145


.2350


.3081


1.3296


.4833


.2201


1.7875


.3760


1.2761


.4222


.0440


1.2155


.3984


.7784


.1551


.7493


.2440


.6226


.1835


.0050


.6487


] .2240


.4605


.0303


1.6592


.5990


] .0374


.1794


.3590


• 8203


,8480


.8019


.6554


1.2212


.5430


1 .0629


.7520


.5980


.1040


1.3424


.4027


.5039


1.6752


.4280


1.2267


.9452


.4600


.7644


.8368


.7929


.4215


1.3384


.8670


1.1044


.6577


.3210


1.0270


. 0944


- .9055


.3529


.4358


.41UU


.5547


.5983


.6920


.4498


.2240


.7549


.3757


.5647


.0410


.6437


.8743


.1950


.8502


.2288


.5437


.5046


.5507


.7940


,5594


.6511


.4510


.7163


.7888


.8199


.4647


1.1573


.4640


.9386


.7863


.9480


.8359


.3184


1.0409


.5190


.7070


.5130


.7644


1.1972


.9800


1.1206


.7712


1.2600


.5730


1.3123


.0440


1.1101


1.2634


.3310


1.1063


.9968


.8100


.6665


1.4570


.4980


1.3494


.8058


.8090


.6630


.0640


.9464


.5741


.4876


,7420


.5560


1.0155


.7970


.6812


1 .4624


.7871


.8872


1.9348


.9660


1.7238


1.2289


.1860


.4329


.4048


.5293


.1634


.6331


.7130


.4404


.2554


.7400


.3822


.6240


.6555


.6393


.9601


.7090


1.0342


.9958


.5410


1.0192


.8976


.8581


.7896


1.3392


.4300


1.2455


1.0399


.1160


.8372


1.5808


.5871


.0956


2.0940


.2750


1.3825


.1797


.483J


.3211


1.2672


.6341


.3543


1.7257


.1000


1.1411


.6886


.6900


.9737


.6608


1.0957


.6608


1.2377


.7630


1.1323


1.0372


.0910


1.1466


.0144


.8338


.4947


.3461


.2700


.5469


,4354



•14a.



1956



1957



1958



1959



I960



1961



1962



1963



1964



Yl



Y2



Y3



Y4



Y5



Y6



Y7



Y8



Y9



43.9839
26.8987
21.6015
29.9612
5 3". 3 1 3 3
35.0625
45.4569
43.2667
23.217-+
39.2643
22.1252
38.9945
22.7928
39.1373
41.1760
35.8769
29.2838
41.5666
50.2241
b8.4803
40.1771
43.1779
39.8651
23.9738
31.1702
3",. 9746
31.3227
31.3383
51.8782
41.3288



45.5353
14,8456

6.9588
29.2960
27,9823
11.5731
49.9092
19.1950
13.2294
11,1314

4.7503
37,2902
26.3480
20.9687
19.3770
21.9876
25.2276
24.7871
31.1850
30.0465
35.3017
30,5874
47,2384
12,0672
33.8918
43.3092

8.3371
21.3163
37.1230
27,2651



68,5929

36,5103
50,2256

9,4317
28.2529
74.4924

5.8536
78.6656
98.9499
43.7069
91.3138
68,4990
92. 1372
77,4018
24,3150
32.4960
33.1479
62.7611
38.4422
76.5329
79.8279
32.0929

7.3759
37.0523
52.5697
77.8703
16.9560
93.8971
72.6357
22.4190



30.6735
27.9180
21.6755
42.0310
41.9650
28.5010
4 5.0945
13.1560
20.2840
16,8190
29,8375
31.1080
22,0990
45,3035
24,6675

5.9565
41,1785
27.1260
26.1635

2.6785
27.9565
39.3910
52.5250
38.9675
39.9905
22.7095
17.6330

7.5460
41.6295
13.3760



52.0452
27.0053
2 7.4610
61.6101
27.3905
49,8895
73.4895
51.9132
58.5375
32.8912
48. 1084
52.3499
57,9301
52,6561
27.8815
32.5848
25.2058
4^,679^+
39.2580
5 2.4413
63.7797
29.7515
77.8430
23.7872
49,9333
57,0965
64,8941
52,3318
54,5413
26,0286



54,7294
27,4753
8,9480
42.3745
36.6623
17.9495
59.3931
31.0051
J7.8623
7,7787
8.9840
34,5961
42.4178
28.0101
28.6377
38.2923
30.1543
32.9778
49.1796
52.0963
32.8496
43,0511
50,5057
10,6154
42,5100
43,4185
10.5242
28,4289


1

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